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Experiments on discrimination

and social norms

Tom Lane

University of Nottingham, Department of Economics

PhD thesis, submitted March 2017

Supervised by Abigail Barr and Daniele Nosenzo

1

Abstract

This dissertation presents three projects within the fields of behavioural and

experimental economics. The first consists of a meta-analysis of lab experiments

measuring economic discrimination. Most importantly, I find that the strength of

discrimination in economics experiments varies depending on the dimension of

identity across which discrimination is measured, and depending on the type of game

used to measure it. The second project investigates the relationship between

discriminatory behaviour and social norms. A lab experiments finds that

discrimination is stronger when it is perceived to be more socially appropriate. In the

third project, a field experiment investigates the effect of different nudges on voter

registration rates. In particular, emphasising the possibility of being fined for failing

to register is successful in raising registration rates, but offering the possibility of

financial gain for registering is not. An online experiment in the same project

suggests the conflicting normative effects of the two nudges may help explain these

differences.

2

Table of contents

3. Chapter One: Introduction

8. Chapter Two: Discrimination in the laboratory: a meta-analysis of economics

experiments

69. Chapter Three: On the social inappropriateness of discrimination

130. Chapter Four: Nudging the electorate: what works and why?

174. Chapter Five: Conclusion

177. Acknowledgements

3

Chapter One: Introduction This dissertation presents three research projects. All three projects fall within the

fields of behavioural and experimental economics, although each uses a different

methodology, the first being a meta-analysis, the second a lab experiment and the

third a combination of field and online experiments. The research questions addressed

also vary, but the two main themes of the dissertation are discrimination and social

norms. The project presented in Chapter 2 focuses on discrimination. The project

presented in Chapter 4 focuses on social norms. And the project in Chapter 3 focuses

on norms of discrimination and how they vary across contexts.

Chapter 2 consists of a meta-analysis of lab experiments measuring economic

discrimination. The chapter, entitled ‘Discrimination in the laboratory: a meta-

analysis of economics experiments’, was published as a paper in the European

Economic Review in 2016. Discrimination has long been regarded as an important

economic matter (at least since Becker, 1957), and experimental research in

economics measuring discrimination has proliferated in the last 15 years or so, since

the emergence of such ground-breaking studies as Fershtman and Gneezy (2001).

However, the results of this experimental literature have often been contradictory, and

a clear consensus has been lacking regarding the types of experimental circumstances

under which particularly strong or weak discrimination should be expected to appear.

Given the now-large available sample of studies, a meta-analysis is an appropriate

tool for addressing this issue, particularly as it is more objective than qualitative

literature review.

The database of experimental results that I harvested was sufficiently large and

diverse to address various questions. In particular, I investigated whether the strength

of discrimination systematically differs according to the type of identity it is based

upon, the type of game-setting in which it is elicited, and the characteristics of the

subjects participating in the experiment. I also investigated whether the experimental

literature provided more support for taste-based or statistical discrimination, and

made male-female comparisons of behaviour in experiments studying gender

discrimination. To maximise the likelihood of yielding unbiased answers to these

questions, two crucial design aspects of the meta-analysis were: 1) ensuring a

4

sufficiently thorough and rigorous literature search was conducted; and 2) deciding

upon and consistently applying a set of criteria to determine which of these identified

studies were included in the final database. Section 2 of the paper addresses these

issues in depth.

A key finding of the meta-analysis was that the strength of discrimination in

economics experiments varies depending on the dimension of identity across which

discrimination is measured. Strikingly, discrimination has tended to be stronger in

experiments with minimal groups (that is, groups whose identities are artificially

induced during the experiment, using procedures similar to those first developed by

Tajfel et al, 1971) than in experiments with groups based on ethnicity, nationality or

religion. The identity type upon which the weakest discrimination has tended to be

found is gender – with, in fact, a slight tendency towards subjects favouring members

of the opposite gender. The strongest levels of discrimination have been found

between groups with identities based on social or geographical characteristics.

Regarding game-setting, I found discrimination tends to be particularly strong in the

‘third-party allocator game’ (where decision-makers are required to allocate payoffs

between passive in-group and out-group members). I found evidence throughout the

literature for the existence of both taste-based and statistical discrimination, but that

taste-based discrimination has tended to play the dominant role. I also found that

levels of discrimination are not significantly affected by whether subjects are students

or non-students and that, in gender experiments, the strength of male-to-female

discrimination has not tended to significantly differ from that of female-to-male

discrimination.

The relative strength of discrimination between groups with artificially-induced

identities may seem counterintuitive: why would ‘minimal’ groups not yield minimal

levels of discrimination? I designate some discussion to this question in Chapter 2,

before attempting to address it empirically in Chapter 3. Chapter 3, entitled ‘On the

social inappropriateness of discrimination’, reports the results of a lab experiment

investigating the relationship between discriminatory behaviour and social norms.

Social norms are increasingly being presented as important determinants of economic

behaviour, particularly within the experimental literature instigated by Krupka and

5

Weber (2013), which attempts to directly measure social norms. We hypothesised

that they might help explain why discrimination is more pronounced in some contexts

than others.

In this experiment, we replicate under controlled conditions the finding from the

meta-analysis that discrimination is stronger across minimal groups than across

groups based on nationality. We did this by measuring discrimination in two

treatments which differed only in the type of group identity primed amongst subjects.

In one treatment subjects were split into groups based upon whether they were British

or Chinese; in the other, they were split into groups on the basis of which colour of

ball they randomly drew from a bag. Consistent with the result of the meta-analysis,

discrimination was found to be significantly stronger in the treatment with minimal

groups.

The experiment also measured the social norms pertaining to discrimination in each

treatment. Following the methodology of Krupka and Weber (2013), we asked

subjects to evaluate the social appropriateness of each action decision-makers in the

experiment could take. This task was incentivised such that subjects whose

evaluations matched those of others would receive money; thus, evaluators were

encouraged to coordinate on the social norms. As we hypothesised, discrimination

was perceived to be more socially inappropriate in the treatment with national groups.

Our results suggest that social norms may affect discrimination and that cross-

contextual variations in the social appropriateness of discriminatory behaviour may

help explain cross-contextual variations in the strength of observed discrimination. In

particular, the relatively strong discrimination observed in minimal group

experiments may be the result of relatively weak social norms against discrimination

in such settings. In the chapter, we discuss how the findings of our experiment are

consistent with a theoretical framework based closely upon that of Akerlof and

Kranton (2000, 2005).

Chapter 4, entitled ‘Nudging the electorate: a field experiment on raising voter

registration for the UK General Election’, reports a field experiment ran in

conjunction with Oxford City Council on the effect of various behavioural

interventions on voter registration rates amongst the UK electorate. The paper is

6

impact-focused, contributing to the literature on nudging (Thaler and Sunstein, 2008)

in public policy. There is also a conceptual focus, as we explore social norms as a

possible mechanism for the success or failure of particular nudges.

In the study, Oxford City Council sent postcards to unregistered student voters,

encouraging them to register to vote ahead of a General Election. The postcards were

designed such that only the wording of the messages on them varied between

treatments, allowing us to isolate the effects on registration of particular persuasion

strategies. Specifically, we tested the effects of emphasising to recipients the

possibility that they could be fined for not registering; of offering potential monetary

rewards, in the form of entry into a lottery to win cash prizes, for recipients who

registered early; and of attempting to nudge recipients towards registering through the

purely psychological means of a foot-in-the-door effect (Freedman and Fraser, 1966).

We found that emphasising the possibility of being fined raised registration rates

substantially. However, offering entry into the lottery had no overall effect on

registration and, once the deadline for the lottery had passed, subjects exposed to this

intervention were in fact significantly less likely to register than those in a control

treatment. Our attempts to invoke the foot-in-the-door effect were also unsuccessful.

Therefore, our study offers clear advice to policymakers on how they should and

should not attempt to raise registration rates.

As we discuss in the paper, there are multiple possible explanations for why

emphasising the fine works well while offering monetary incentives for registering

does not. We empirically explore one of these: the effect of each intervention on

social norms. In a follow-up study, we investigated the effects of being exposed to

each intervention on the perceived social appropriateness of registration behaviour,

again using the incentivised norm-elicitation method of Krupka and Weber (2013).

Exposure to the postcard emphasising the possibility of a fine strengthened the

perceived social norm that one should register to vote, while exposure to the postcard

offering entry into the lottery weakened it. We suggest that this strengthening of the

norm may have contributed to the success of the fine treatment, while the weakening

of the norm may help explain why, as in some previous economic research (e.g. Frey

7

and Oberholzer-Gee, 1997), the offer of monetary rewards may crowd out people’s

intrinsic motivation to engage in a socially beneficial act.

References

Akerlof, G. A., & Kranton, R. E. (2000). Economics and identity. Quarterly Journal

of Economics, 715-753.

Akerlof, G. A., & Kranton, R. E. (2005). Identity and the Economics of

Organizations. Journal of Economic Perspectives, 9-32.

Becker, G. S. (2010). The economics of discrimination, University of Chicago press.

Fershtman, C., & Gneezy, U. (2001). Discrimination in a segmented society: An

experimental approach. Quarterly Journal of Economics, 351-377.

Freedman, J. L., & Fraser, S. C. (1966). Compliance without pressure: the foot-in-the-

door technique. Journal of personality and social psychology, 4(2), 195.

Frey, B. S., & Oberholzer-Gee, F. (1997). The cost of price incentives: An empirical

analysis of motivation crowding-out. The American economic review, 87(4), 746-755.

Krupka, E. L., & Weber, R. A. (2013). Identifying social norms using coordination

games: Why does dictator game sharing vary?. Journal of the European Economic

Association, 11(3), 495-524.

Tajfel, H., et al. (1971). "Social Categorization and Intergroup Behavior." European

Journal of Social Psychology 1(2): 149-177.

Thaler, R. H., & Sunstein, C. R. (2008). Nudge: Improving Decisions About Health,

Wealth, and Happiness. Yale University Press.

8

Chapter Two: Discrimination in the

laboratory: a meta-analysis of

economics experiments

Abstract

Economists are increasingly using experiments to study and measure discrimination

between groups. In a meta-analysis containing 441 results from 77 studies, we find

groups significantly discriminate against each other in roughly a third of cases.

Discrimination varies depending upon the type of group identity being studied: it is

stronger when identity is artificially induced in the laboratory than when the subject

pool is divided by ethnicity or nationality, and higher still when participants are split

into socially or geographically distinct groups. In gender discrimination experiments,

there is significant favouritism towards the opposite gender. There is evidence for

both taste-based and statistical discrimination; tastes drive the general pattern of

discrimination against out-groups, but statistical beliefs are found to affect

discrimination in specific instances. Relative to all other decision-making contexts,

discrimination is much stronger when participants are asked to allocate payoffs

between passive in-group and out-group members. Students and non-students appear

to discriminate equally. We discuss possible interpretations and implications of our

findings.

JEL classifications: C92 – Laboratory Experiments (Group Behaviour); D03 –

Behavioural Microeconomics: Underlying Principles

Keywords: Discrimination; Meta-analysis

9

1. Introduction

Meta-analysis – a commonplace technique in medical science, psychology and, to a

growing extent, economics – holds advantages over literature review in terms of

objectivity and analytical rigour. In recent years, the experimental economics

literature appears to have reached a critical mass at which researchers are finding

meta-analyses useful.1 The benefit of these works is that, by aggregating data across a

large number of experiments and exploiting natural between-study design variation,

they pinpoint behavioural regularities and the variables that modify them more

precisely than could be done through qualitative review.

We run a meta-analysis on the body of studies investigating discrimination in

lab and lab-in-the-field experiments, a sub-literature which has certainly reached the

necessary critical mass for such a venture. Economists’ interest in discrimination has

been strong ever since Becker (1957), and with the growth of experimental

economics in the last two decades, experiments have emerged as a popular

complement to survey-based econometric studies.

These experiments create a controlled environment and therefore allow much

cleaner measurements of discrimination than the analysis of naturally-occurring data,

avoiding such problems as omitted variable bias and reverse causality. Furthermore,

by testing for a very fundamental and general form of discrimination – simply,

whether subjects treat others differently depending on which group those others

belong to – experimental economists can produce findings of interest not only to their

own discipline but also across the social sciences. Also, through the use of incentives,

experiments hold a key advantage over questionnaire-based measures of

discrimination, in that they elicit revealed rather than reported discrimination.

1 Several meta-analyses of economics experiments have been released in recent years, including:

Engel (2007) – oligopoly experiments; Prante et al. (2007) – Coasean bargaining; Jones (2008) –

group cooperation in prisoners’ dilemmas; Hopfensitz (2009) – the effects of reference

dependence and the gambler’s fallacy on investment; Percoco and Nijkamp (2009) – time

discounting; Weiszäcker (2010) – social learning; Engel (2011) – dictator games; Johnson and

Mislin (2011) – trust games.

10

Psychologists had already been studying discrimination in the lab for decades,

and experimental economists have drawn on their knowledge, particularly regarding

the minimal group paradigm. This technique was first introduced by Tajfel et al

(1971) and has spawned a huge body of experiments wherein group identity is

artificially induced in the laboratory. This is often done by, in a preliminary phase of

an experiment, asking subjects to state their preference for one artist over another, or

to randomly draw a colour. The experimenter then splits the subject pool into groups

according to their art preference, or the colour they have drawn, and makes it known

to participants that the division is based on these differences. Subsequent stages of

such experiments involve interaction tasks between the groups and find

discrimination surprisingly (at least to the early researchers) often.

To study discrimination, experimental economists set up games such as the

dictator game, the trust game or the prisoner’s dilemma, and invite a subject pool

segregated along the lines of a particular identity-based characteristic (or else

generate this segregation with artificial groups). They make subjects aware of the

group affiliation of those they interact with, and then measure how their behaviour

varies according to whether individuals they are interacting with share their identity

(are in-group) or do not (are out-group).

The number of economics experiments of this type has grown rapidly since

the turn of the century and now encompasses substantial diversity across several

dimensions. Even after omitting many papers which investigate discrimination but do

not meet our inclusion criteria devised to ensure a consistent approach (see Section

2), we are left with a dataset consisting of 441 experimental results (significant and

null) from 77 studies – more data than most of the other experimental economics

meta-analyses have had. In order to aid the progression of this literature, it is worth

taking stock of what has been found to date, particularly as casual inspection reveals

non-uniformity in the results; the strength of discrimination found against out-groups

varies considerably, and some experiments even find discrimination in the opposite

direction, i.e. against the in-group.

The aim of this meta-analysis is both to yield broad insights on discrimination

and to inform the designers of future experiments testing for it. We first investigate

11

the average strength of discrimination across the literature. We then inquire how it

tends to vary according to specific experimental characteristics.

In particular, we are interested in whether the strength of discrimination

depends on the type of identity being investigated. Comparing the level of

discrimination between artificial (i.e. minimal) groups and various types of natural

groups (such as those based on ethnicity, nationality, religion, gender and

social/geographical affiliation) is particularly interesting. One might expect ‘minimal’

groups to yield minimal levels of discrimination. However, it is also conceivable that

artificial identity inducement confers an experimenter demand effect in favour of

discrimination, or that the experimental priming of sensitive natural identities reduces

subjects’ desire to discriminate owing to a preference not to engage in socially

unacceptable behaviour. Evidence for these possibilities, in the form of relatively

strong discrimination in artificial group experiments, could have implications for the

external validity of certain experiments.

A further interesting question is whether the strength of discrimination varies

according to the type of decision subjects are asked to make. This has implications in

terms of the real-world circumstances in which discrimination can be most expected

to appear and for the generalisability of findings.

We further ask whether experiments with students reveal greater or lesser

discrimination than those with non-students. This is also important for the external

validity of findings, and is a question worth pursuing as some studies (e.g. Bellemare

and Kroger, 2007; Anderson et al, 2013) have found students are not entirely

representative of wider populations in economics experiments.

This meta-analysis also aims to shed light on the motivations behind

discrimination. Some experiments have been designed specifically to distinguish

between taste-based discrimination and statistical discrimination – the two models

that continue to dominate the theoretical literature in economics. The taste-based

model, proposed by Becker (1957), entails individuals gaining direct utility from the

act of discriminating against out-groups. Meanwhile, according to theories of

statistical discrimination – beginning with Arrow (1972) – individuals aim to

maximise their own payoffs given their beliefs and expectations about others’

12

characteristics and behaviour, and discrimination occurs when those beliefs and

expectations vary depending on the group to which the others belong. Understanding

the relative importance of these two motivations will improve the focus of future

research and the design of policies aimed at combating discrimination.

Finally, we include a subsection on experiments investigating gender

discrimination. Gender is unique amongst the identity types in having the same two

groups in each experiment. It is therefore simple to make a clean comparison between

male-to-female discrimination and female-to-male discrimination.

In summary, the meta-analysis presented below aims to address the following

questions: (1) What is the general pattern of discrimination across the literature? (2)

How does the level of discrimination vary according to the type of identity groups are

based upon? (3) How does the level of discrimination depend upon the decision-

making context? (4) Do students discriminate any more or less than non-students? (5)

Does the experimental literature provide more support for taste-based or statistical

theories of discrimination? (6) In gender experiments, how does male-to-female

discrimination compare with female-to-male discrimination?

Our main results, presented in Section 3, are as follows. (1) We find a

moderate tendency towards discrimination against the out-group, with a majority of

null results across the literature. (2) The strength of discrimination against the out-

group does vary according to the type of group identity subjects are divided by. It is

greater when identity is artificially instilled in a subject pool than when it is divided

by nationality or ethnicity – minimal groups, it seems, are not so minimal after all.

Discrimination is even stronger, though, when participants are divided into socially or

geographically distinct groups. (3) The extent of discrimination against the out-group

also depends on the role participants are given in an experiment: when subjects are

asked to allocate payoffs between inactive players belonging to the in-group and out-

group, it is stronger than in any other decision-making context. (4) Students do not

appear to be differently inclined towards discrimination than non-students. (5) We

find evidence in support of both taste-based and statistical discrimination. Tastes

appear to drive the general tendency for discrimination against the out-group, but

individual studies have found beliefs to affect discrimination. (6) In gender

13

discrimination experiments the tendency for discrimination against the out-group is

reversed, as subjects demonstrate slight but significant favouritism towards the

opposite gender. Discriminatory behaviour in these experiments does not differ

significantly between males and females. We discuss possible interpretations of these

results in depth in Section 4.

We are aware of only one other meta-study attempting to analyse the

experimental discrimination literature – Balliet et al (2014)2, who take 214 estimates

of discrimination from 78 studies. There is little overlap between our samples; Balliet

et al take studies from across the social sciences but their search and inclusion criteria

result in most of the experimental economics literature on discrimination not being

included (26 of our studies – around a third – feature in Balliet et al’s sample). They

exclude decision-making contexts which we consider, such as being the second mover

in a sequential game or a third-party allocator. They also exclude interactions between

gender groups.

The present study and that of Balliet et al can be viewed as complements.

Through focusing only on economic experiments, we enhance comparability and

eliminate some studies using methodological elements that may not be acceptable to

some social scientists. Our focus on the economic theories of taste-based and

statistical discrimination differentiates our study from Balliet et al, who investigate

2 Although nothing approaching a full meta-analysis of the in-group-out-group literature had

previously been conducted, several social psychology meta-studies have investigated specific

phenomena within it. Saucier et al (2005) analysed research measuring the degrees to which

subjects would help white and black people; while not finding statistically significant aggregate

discrimination against black people, they showed it increased in emergency situations and cases

where helping was more difficult or risky. Bettencourt et al (2001) found high-status groups

exhibited more in-group bias than low-status groups. Fischer and Derham (2010) concluded

discrimination in minimal group experiments was stronger in countries whose societies are

considered more individualistic. Aberson et al (2000) found greater in-group bias amongst

individuals with higher self-esteem. Robbins and Krueger (2005) found social projection, ‘the

tendency to expect similarities between oneself and others’, to be stronger towards in-groups

than out-groups, and that this effect was amplified with artificial groups relative to natural ones.

Although interesting, many of the studies included in these meta-analyses are considerably

different from those we consider – often they do not relate specifically to economic behaviour,

and even if they do they may not be incentivised.

14

psychological theories of discrimination. Throughout our analysis we compare our

results to theirs. Their paper finds a similar overall tendency for discrimination to

what we do. They find the extent of discrimination not to differ significantly between

settings of natural and artificial identity, but do not split natural identity into

subcategories as we do. The clearest difference in results between the two studies is

that Balliet et al find discrimination is stronger by decision-makers who move

simultaneously than by first movers in sequential exchanges, while we do not find it

significantly differs between these settings.

2. Methodology and criteria for inclusion

We chose to restrict our study to the experimental economics literature. Almost all of

the economics experiments have been conducted in the last 15 years and can

reasonably be expected to have followed comparable procedures, which is important

in a meta-analysis. We define an economics paper as follows: it must either have been

published in an economics journal or have as at least one of its authors a person

trained in economics or a business-related discipline, or who has at least once held a

position in an economics or business-related department. Furthermore, we exclude

economics papers which, it is clear to the reader, exhibit a breach of standard

experimental economics practice – most notably, deception. For inclusion, an

experiment must involve interaction between individuals whose decisions determine

real material payoffs for participating players. In other words, it must be incentivised.

A serious pitfall meta-analyses can face is publication bias, also named the

‘file drawer problem’. Because null results are less likely to be published than

significant ones, a meta-analysis risks including a disproportionately low number of

studies finding small or no effects (Rosenthal, 1979; Rothstein, 2006). This can lead

to an overestimation of average effect sizes. It can also, if null results are particularly

unlikely to be published when combined with certain other features of a study, result

in the meta-analysis overestimating the relationship between strong effects and these

features; in our case, for instance, if null results in trust games were never published

but null results in other games sometimes were, we would be in danger of estimating

a spuriously strong relationship between trust games and significant results. To

15

minimise such bias, a good meta-analysis should conduct the most thorough literature

search possible in order to find all applicable studies, whether published or not. Our

approach was threefold. In late 2013, we conducted RePEc searches for the

keywords, ‘Discrimination experiment’, ‘Identity experiment’, ‘Ingroup experiment’

and ‘Outgroup experiment’, and carefully sifted through the output for candidate

studies. We then followed the references and citations of all papers identified as

relevant. Finally, we checked our list of included studies against that of Balliet et al

(2014); this step added one study (Spiegelman, 2012).3 One feature of the literature

we meta-analyse is that studies tend to include various different treatments, and

therefore report multiple results. This may act as a further curb on publication bias –

insignificant findings make their way into papers alongside more interesting

significant results (indeed, it turns out the majority of results in our dataset are null).4

Previous meta-analyses in experimental economics such as Engel (2011) and

Johnson and Mislin (2011), which focus on a single game type, are able to use the

average behaviour of subjects (amount sent in the dictator or trust game) as a

continuous dependent variable, with one observation and an associated standard error

for each treatment. In our case, we are pooling across different game types and

therefore need a way of transforming the data to make meaningful comparisons

between these settings. Our variable of interest is the difference between decision-

makers’ behaviour towards their in-group and their out-group, whilst all other aspects

of the experimental design are held constant – in essence, the discrimination effect

size. There is typically one observation per every two treatments (one in-group and

one out-group treatment) for each type of player active in the given game. The

exception is when a decision-maker interacts with both the in-group and the out-

group in the same treatment (either by making one decision which simultaneously

3 The Balliet et al project was not in the public domain when we embarked upon ours, and we were

unaware of it. We designed our search and inclusion criteria independently of theirs. However,

learning of their meta-analysis provided the perfect opportunity to test the thoroughness of our

search for studies. That Balliet et al include only one study which fits our inclusion criteria but

which we had not independently found suggests it is unlikely we have missed many applicable

papers.

4 The number of observations generated by a single paper varies from 1 to 24, with Chen et al

(2014) providing the most.

16

affects both, or by playing in the same role twice), in which case a within-treatment

measure of discrimination is available.5 The ideal approach would be to record an

effect size for each comparison, and we attempt to do this. Consistent with Balliet et

al (2014), the measure we use is Hedges’ unbiased d: the mean difference in

behaviour towards the in-group and the out-group, divided by the pooled standard

deviation, with a minor correction for sample size (Hedges and Olkin, 1985).

However, a substantial number of studies do not report sufficient data for us to

calculate effect sizes. This is particularly the case with null results, as when a

difference is not significant authors are less likely to report the test statistic from

which an effect size could be derived. We sent data requests to the authors of all

papers for which we could not construct the measure using information provided in

the paper. After receiving data from 22 of the 36 sets of contacted authors, we ended

up with effect sizes on 364 of our 441 data-points. We therefore also employ a binary

dependent variable, recording simply whether, for each comparison, behaviour

significantly favours the in-group over the out-group at the 5% level.6 The effect size

is the inferior dependent variable in that it restricts the sample and may lead to greater

under-representation of null results; but the superior one in terms of information

content.

For simplicity, we define ‘discrimination’ as discrimination against the out-

group, and ‘out-group favouritism’ as discrimination against the in-group, and will

use these terms hereafter. Unlike some, we make no distinction between nepotism and

discrimination; any result of favouritism towards one group relative to a second can

equivalently be interpreted as discrimination against the second group. We therefore

conceptualise ‘discrimination’ (against the out-group) as something which can be

5 For a game to meaningfully measure discrimination, and therefore for us to include it, it must be

possible to unambiguously rank the decision-maker’s available actions in terms of how favourable

they are to the decision-maker’s partner. Certain coordination games cannot be included, since

whether one action is more favourable depends upon the move a partner simultaneously makes.

In Appendix A, Table A.2 we list all the game types included in our sample, and explain how they

measure discrimination.

6 We also do this for out-group favouritism, recording whether or not behaviour significantly favours

the out-group over the in-group at the 5% level, and run separate regressions on this. These are

reported in Appendix C, Table C.1.

17

measured on a continuum with positive and negative values. When discussing

average effect sizes, we will describe a relatively low value as indicating ‘lower’ or

‘weaker’ discrimination, even if it is driven by highly negative effect sizes (i.e. even

if it is driven by instances of strong discrimination against the in-group).

For an observation to meet our inclusion criteria, there must be an in-group

and out-group, clearly defined on the basis of categorisation by a discrete identity-

relevant variable, such as ethnicity, gender or – as with artificial groups – the

preference for a particular artist or the colour randomly drawn. There must be

controlled interaction within and between the groups, and decision-makers must be

aware that they are interacting with individuals belonging to their in-group or out-

group. We only consider an in-group to be appropriately defined as such if every one

of its members shares the same categorisation as the decision-maker on the basis of

the relevant variable. For an out-group to be appropriately so-defined, every member

must take a different categorisation from the decision-maker. It is not required that all

members of an out-group take the same categorisation as each other. For instance,

Guillen and Ji (2011) use as their two groups Australian and non-Australian. In this

case, for an Australian decision-maker the Australians are the in-group and the non-

Australians the out-group, but for a non-Australian the other non-Australians should

not count as their in-group. We then only record the observed behaviour of the

appropriately defined group, the Australians in this example. Occasionally, we are

forced to make a subjective decision on what can reasonably be considered a group.

For example, from Chen et al (2011), which splits its US-based sample into white and

Asian students, we record the behaviour of the white ‘group’ but not that of the

Asians, as we believe that in American society white people can appropriately be

defined as comprising a shared ethnicity, whilst those of Asian descent comprise a

mixture of ethnicities.7 Papers such as Falk and Zender (2007) which do not have

clear groups but measure each subject’s position on a scale of social distance, based

on a continuous variable, are not included.

7 There were four cases where we made such subjective decisions, all listed in Appendix A. Our

main results still hold regardless of the decisions we come to in these cases.

18

If an experimental design splits the sample up into more than two separate

groups, on the basis of a single identity-relevant variable, we record separately how

each group treats each other group relative to its own. If such a paper reports that

Group A does not significantly discriminate against Group B or Group C but does

significantly discriminate against Groups B and C combined, we record two results of

no discrimination rather than one result of discrimination; and in the main text of this

paper we report our results using this approach. We do this because, although Groups

B and C combined could represent a single out-group as defined above, the

experiment was set up to treat them as separate out-groups. Similarly, we do not

include the reported results of statistical tests run on data pooling two or more

treatment pairs. These are grey areas but we have re-run our main regression results

for the binary dependent variables in the case of treating every result reported in our

sample as an observation: this adds 16 extra data-points and does not qualitatively

change our findings.

Sufficient data must be reported for it to be clear whether there is significant

discrimination in each pair of treatments (or, when applicable, single treatment); if we

cannot work out whether there is discrimination in one or more treatment pair, the

whole paper is omitted from the study. This is because papers are less likely to report

the results of statistical tests finding no discrimination, and if we failed to include a

given study’s non-results our analysis would overestimate the likelihood of this

particular design finding discrimination. For similar reasons, if an experiment

employs a cross-cutting design, dividing its subject pool by multiple identity types, it

must report whether there is discrimination on the basis of each category. For

example, an experiment which segregates the subjects by both gender and ethnicity

must report, for each applicable treatment pair, whether each ethnic group

discriminates against each other ethnic group or not, and also whether each gender

discriminates against the other or not. Otherwise, we omit the study.

Experimenters using artificial groups generally conduct tests on pooled data;

rather than reporting whether Group A discriminates against Group B and vice versa,

they report whether individuals across the sample pool discriminate against out-group

members. This makes sense because there is no obvious reason to doubt the

relationship between two artificial groups is completely symmetrical. As such, we use

19

pooled discrimination observations for artificial group experiments. Using similar

reasoning, we also admit pooled discrimination observations for experiments dividing

subjects by their real-world social groups. The pooling of certain types of data might

lead to an increased chance of finding discrimination in certain experiments, which is

one reason why we use the size of the sample from which the result is derived as a

control variable in our regression analysis.

We limit our analysis to lab and lab-in-the-field experiments; we do not

include pure field experiments, in which subjects do not know they are participants in

a study. We therefore do not include the large body of field experiments in which

applications are sent to employers, landlords or others to test for discrimination in

markets (correspondence studies).

2.1 Analytical methods

Listed in the next subsection are descriptions of the independent variables we include

in our regressions. Our basic model contains role and identity type dummies, and

some controls. Because our samples are not large and most variables are dummies, we

regard linear probability models (LPMs) with errors corrected for heteroskedasticity

as the best specifications when employing the binary dependent variables. However,

we also run as robustness checks logit models, which we report in Appendix C, Table

C.2. In some cases the logits drop observations, which is a major disadvantage. Their

results, however, are qualitatively similar to the LPMs. When using binary dependent

variables, we treat each study within the meta-analysis as providing a cluster of

observations.

When analysing the continuous dependent variable, we first use standard

random effects meta-analysis procedures to determine average effect sizes for our full

sample and for the subsamples based on identity type. These are simply aggregate

estimates for the level of discrimination in the relevant subsample; they do not control

for independent variables. The procedure takes into account that each observation has

an associated standard error. It weights each observation by the inverse of this

standard error, thus attaching more importance to results from larger samples and

20

with smaller standard deviations. It then follows an unweighting process, the extent of

which depends upon the heterogeneity in effect sizes. The more heterogeneity there is

across effect sizes, the more equal will be the weights attached to observations with

small or large standard errors (Harbord and Higgins, 2008).8

We then apply random effects meta-regressions, which allow the inclusion of

independent variables in the analysis. These models follow the same processes of

weighting and unweighting observations as described in the previous paragraph, but

are otherwise standard linear regressions. Whereas with the binary dependent variable

we must approach discrimination and out-group favouritism separately, the meta-

regression analyses both simultaneously, since the effect sizes can be positive or

negative. This can be one reason why the results of the meta-regressions may differ

from those of the linear probability regressions. Another can be the reduction in

sample – therefore, when the results of the meta-regressions do not match those of the

LPM regressions on discrimination , we present the LPMs re-run on the reduced

effect-size sample, in order to determine whether the disparity is due to the change in

sample or the change in analytical approach.

2.2 Independent variables

Role type dummies: We include role type dummy variables to pursue the question of

how different decision-making contexts affect the extent of discrimination. The

games used in this literature feature either multilateral or unilateral decision-making.

When decision-making is multilateral, the outcome of the game is determined by

more than one player’s actions. From such situations, we identify three different role

types: First Mover (140 observations), where one’s move does not finish the game;

Second Mover (119 observations), where one determines the final payoffs in response

8 The random effects approach is more suitable for our purposes than the fixed effects alternative,

which excludes the unweighting step; the fixed effects process assumes there to be one true effect

size across all studies, while random effects allow it to vary – the latter seems more plausible in

our case, as we do not assume discrimination to be a universal constant.

21

to the co-player(s)’ actions; and Simultaneous Mover (66 observations), where one

makes the last move of the game at the same time as one’s co-player(s).

When decision-making is unilateral, the final outcome of the game is

determined by one player. From these situations, we identify a further three role

types. First, there is the Dictator (67 observations), who allocates payoffs between

another player and his- or herself. Next we have third-party allocators (Allocator, 30).

These are players who must divide a pie between two or more passive players (who,

in these experiments, are members of different groups), but whose own payoff does

not depend on this decision. Finally, there are players tasked with selecting a partner

(from a choice of in-group and out-group participants) with whom to play a

subsequent game. We label this role Partner Chooser (19 observations).9

Identity type dummies: A second set of dummy variables records which type of

group identity a given experimental sample has been divided according to. We

consider identity to have been artificially induced if researchers split subjects into

groups that, prior to the experiment, did not exist – in the sense of group members

sharing characteristics that are not also shared by members of other groups in the

study – and the subjects are aware they have been split into these groups.10 49 studies

in the meta-analysis investigate natural identity, 32 artificially generate it, while the

remaining four contain both natural and artificial treatments. We have 272

observations for natural identity types and 169 for artificial. We subdivide the natural

observations into six specific categories of natural identity.

First, we have 82 observations from 13 studies in which subjects are divided

by Nationality. Next, nine studies investigate Ethnicity-based identity, adding 63

9 We ran further regressions in which we categorised the role types differently. In these models,

dummy variables were assigned to specific game settings, such as the trust game sender and the

trust game returner. The results are reported in Appendix B.

10 There is some inconsistency in the literature on the definition of 'minimal groups'; some authors

(e.g. Chen and Chen, 2011) categorise certain artificial groups as ‘near minimal’. For our purposes,

we use ‘minimal groups’ synonymously with 'artificially created groups.' In Appendix B, we explore

the effects of inducing artificial identity using different methods, and show that it seems not to

matter precisely how ‘minimal’ the groups are.

22

observations. A further seven studies generate 32 observations on Gender identity. 21

more observations are provided by five studies in which the subjects are split by

Religion. 13 studies use a rather different approach, dividing the subject pool into

groups based on real-world social and/or geographical identity. This is done in a

variety of ways: for instance, using villages (Dugar and Shahriar, 2009), colleges

within universities (Banuri et al, 2012) or friendship groups (Brands and Sola, 2010).

However, all such designs share the common feature that each decision-maker has a

clearly distinct social and/or geographical in-group – group identity here is defined

with reference to the relative frequency with which one interacts with in- and out-

group members in ordinary life. The 57 observations generated by these experiments

are coded under the variable Soc/Geo Groupings. The remaining 17 results, from four

papers, deal with other types of natural identity, which cannot appropriately be fitted

into the above categories. These observations relate to political identity (Abbink and

Harris, 2012), disability (Gneezy et al, 2012), caste (Hoff et al, 2011) and whether

farmers are private or members of cooperatives (Hopfensitz and Miguel-Florensa,

2013). We pool them under the composite variable Natural Other11.12

Other variables: In our regressions we include as a dummy variable (Students)

whether each observation derives from a sample consisting predominantly of students

or non-students. Even if not explicitly stated, we assume experiments run at

universities have at most a very small number of non-student participants. Likewise,

while we accept experiments in the field may include a few student subjects, their

proportion is likely to be low (unless otherwise stated). As another control, we

include the size of the active decision-making sample from which a given result is

derived (Sample Size).

11 The distinction between Soc/Geo Groupings and Natural Other is not arbitrary: in- and out-groups

in the Natural Other category are not necessarily socially or geographically distinct. However, if the

Natural Other observations are incorporated into the Soc/Geo Groupings category, the Soc/Geo

Groupings coefficients do not change substantially and all other results discussed in the paper

remain unaffected.

12 Two papers provide separate results on more than one natural identity category.

23

3. Results

3.1 What is the general pattern of discrimination across the literature?

In total, as shown in Figure 1, there are 144 results indicating significant

discrimination (32.65%), 28 indicating significant out-group favouritism (6.35%), and

269 indicating no significant discrimination or out-group favouritism (61.00%). 57 of

our 77 studies record at least one result of discrimination, while only 15 record any

results of out-group favouritism. 10 studies separately record results of discrimination

and out-group favouritism. The general tendency, then, leans towards insignificant

results, although only 15 studies consist entirely of nulls.

Figure 1: Breakdown of data-points by result type

Note: Blue bars show the percentage of observations in our dataset which find significant

discrimination (at the 5% level), a null result, and significant out-group favouritism (at the 5% level). Red

points show the average effect sizes for observations belonging to each category.

For the sub-sample where we are able to generate effect sizes (364 of 441

observations), the random effects meta-analysis finds an overall effect size of 0.256

-0.6

-0.4

-0.2

0

0.2

0.4

0.6

0.8

0

10

20

30

40

50

60

70

Find discrimination Null finding Find out-groupfavouritism

Co

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itio

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eff

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siz

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24

(95% confidence range: 0.209 - 0.304). This can be interpreted as, on average,

subjects’ discriminating against out-groups by about a quarter of a standard deviation.

This is not significantly different from Balliet et al (2014), who find an overall effect

size of 0.32 (95% confidence range: 0.27 – 0.38). Figure 1 also displays point

estimates for aggregate effect sizes, conditional on the type of result found for each

observation. Observations finding significant discrimination have an average effect

size of 0.67, those yielding null results have an average effect size of 0.11, and those

finding significant out-group favouritism have an average effect size of -0.51; this

confirms that the strength of the effect size tends to be closely related to the type of

result found for a given observation.

Result 1: In general, there is limited discrimination against the out-group.

3.2 How does the level of discrimination vary according to the type of identity

groups are based upon?

Table 1 displays a breakdown of our sample’s observations by identity category, and

the results of random effects meta-analyses run on these sub-samples. For most

categories the tendency is towards null results. Only for Soc/Geo Groupings – which

yields no results of out-group favouritism – are observations of discrimination more

likely than insignificant results, and this is also the identity type with the highest

average effect size. The category for which there is least discrimination and most out-

group favouritism is gender; the average effect size for this sub-sample is negative.

Table 2a extends the analysis of Table 1 through the use of regressions. LPMa

is a linear probability model with the dependent variable discrimination against the

out-group (equal to 1 if discrimination is found, 0 otherwise). Metareg is a meta-

regression with the dependent variable the discrimination effect size. In both models

artificial identity and the dictator game are the benchmark categories13. In these

13 By necessity, the choices of omitted categories are somewhat arbitrary – there are no variables to

serve as obvious baselines for comparison. We selected Artificial because we regard comparisons

between discrimination with artificial and natural forms of identity to be particularly interesting

(as discussed in Section 1). For role type; we selected Dictator because it is a commonly used

25

regressions we test whether our identity-type variables still yield significantly

different levels of discrimination after controlling for other factors. Table 2b presents

the results of linear restriction tests run on the sets of dummy variables featuring in

the models.

Table 1: Breakdown of data-points by result type and identity type

Category Obs. Find discrimi-nation (%)

Find null (%)

Find out-group favouritism (%)

Obs. with available effect sizes

Average Effect size (d) (with 95% C.I. below)

Artificial 169 42.0 55.6 2.4 150 0.365 (0.279 – 0.450)

Natural National 82 18.3 68.3 13.4 52 0.164 (0.042 – 0.286)

Ethnic 63 11.1 82.6 6.3 59 0.134 (0.013 – 0.255)

Gender 32 9.4 65.6 25.0 28 -0.177 (-0.301 – -0.053)

Religious 21 14.3 80.9 4.8 21 0.034 (-0.062 – 0.131)

Soc/Geo Groupings

57 64.9 35.1 0.0 51 0.551 (0.432 – 0.669)

Natural Other 17 47.1 52.9 0.0 7 -0.036 (-0.158 – 0.086)

Notes: Table 1 shows, for each identity type: the number of observations in our dataset; the percentage

of these observations that find significant discrimination (at the 5% level), null results, and significant

out-group favouritism (at the 5% level); the number of observations for which effect sizes are calculable;

and the weighted average effect size across such observations, with associated 95% confidence

intervals.

In both the linear probability models and meta-regression, the identity

category linked to the strongest discrimination is social and geographical groupings.

In Metareg it yields significantly higher discrimination, at the 1% level, than any of

the other identity categories. In LPMa it does the same, except that the differences

with Artifical and Natural Other are only significant at the 5% and 10% level

respectively.

The identity category linked to the weakest discrimination is gender. Both the

linear probability model and the meta-regression indicate weaker discrimination

game in experimental economics and arguably the simplest, making it a useful object for

comparison.

26

between genders than between artificial groups, significant at the 1% level. The meta-

regression also finds gender discrimination to be weaker than ethnic and national

discrimination (at the 1% level), and religious discrimination (at the 10% level).

However, LPMa does not find these differences to be significant.14

In LPMa the coefficients on the ethnic and national identity types are

significantly negative at the 1% level, strongly indicating that discrimination is less

likely to be observed when subject pools are split along these lines than on the basis

of artificial identities. According to Metareg, however, ethnic and national identity

experiments are only linked to significantly lower discrimination (i.e. less positive

effect sizes) than artificial group experiments at the 10% level.

Given the inconsistency, Table 2a also reports LPMb, a linear probability

model run on the reduced sample for which effect size calculation is possible. This

helps to distinguish whether the losses of significance when moving from LPMa to

Metareg are due to the reduction in sample or the change in measurement technique.

For the comparison of national and artificial identity, the loss of significance appears

to be due to the change in sample, as in LPMb the coefficient is also insignificant.

The same cannot be said for Ethnicity, however, as the linear probability model on the

reduced sample continues to report significantly less discrimination between ethnic

than artificial groups at the 1% level. Doubt, therefore, is cast over the robustness of

14 Gender is also found to be significant in a linear probability regression with out-group favouritism

as the dependent variable, presented as LPMa1 in Appendix C, Table C.1. Our results show that

gender experiments are more likely to yield observations of out-group favouritism than all other

identity types except Nationality, with all differences significant at the 1% level. This model

additionally finds experiments with socially or geographically distinct groups are less likely to

provide results of out-group favouritism than those with artificial or national groups. Other

identity types are not associated with significantly strong or weak out-group favouritism –

however, we have few results of out-group favouritism across our sample. Where we do find

significant identity type effects on out-group favouritism, they are in directions consistent with the

results on discrimination – when an identity type is positively (negatively) associated with out-

group favouritism, it will be negatively (positively) associated with discrimination.

27

Table 2a: Linear probability regressions on discrimination and meta-regressions

on effect size

Dependent variable Discrimination d

LPMa LPMb Metareg

Identity

Ethnicity -0.293*** -0.294*** -0.140*

(0.067) (0.070) (0.079)

Religion -0.235* -0.256* -0.164

(0.131) (0.144) (0.125)

Nationality -0.240*** -0.163 -0.145*

(0.079) (0.099) (0.075)

Gender -0.312*** -0.335*** -0.456***

(0.068) (0.072) (0.099)

Soc/Geo Groupings 0.252** 0.229* 0.354***

(0.099) (0.122) (0.089)

Natural Other -0.056 -0.243 -0.236

(0.165) (0.197) (0.192)

Role Types

First Mover -0.033 -0.025 0.136*

(0.074) (0.081) (0.079)

Second Mover -0.079 -0.066 0.050

(0.065) (0.075) (0.085)

Simultaneous Mover 0.015 0.023 0.095

(0.102) (0.117) (0.095)

Allocator 0.371*** 0.408*** 1.077***

(0.094) (0.140) (0.155)

Partner Chooser 0.070 0.118 0.110

(0.108) (0.113) (0.127)

Controls Students 0.005 -0.025 0.086 (0.063) (0.076) (0.077) Sample Size 6.6e-4 4.9e-4 6.6e-4 (4.8e-4) (7.2e-4) (4.8e-4) Constant 0.406*** 0.422*** 0.144* (0.089) (0.104) (0.105)

R2 (adjusted in Metareg) 0.201 0.196 0.240 N 441 364 364

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa is linear probability model run on full sample, Metareg is meta-regression run on sample for which effect sizes are available, LPMb is linear probability model run on same sample as Metareg; omitted categories are Dictator (role type) and Artificial (identity); errors in LPM models are corrected for heteroskedasticity, with 77 clusters in LPMa and 67 in LPMb; standard errors in italics.

28

Table 2b: Linear Restriction Tests on models presented in Table 2a

Null Hypothesis

P Value on two-tailed test

LPMa LPMb Metareg

Identity

Ethnicity = Religion 0.662 0.776 0.848

Ethnicity = Nationality 0.533 0.201 0.952

Ethnicity = Gender 0.785 0.556 0.007***

Ethnicity = Soc/Geo Groupings <0.001*** <0.001*** <0.001***

Ethnicity = Natural Other 0.144 0.786 0.612

Religion = Nationality 0.973 0.545 0.889

Religion = Gender 0.573 0.582 0.059*

Religion = Soc/Geo Groupings <0.001*** 0.001*** <0.001***

Religion = Natural Other 0.365 0.951 0.719

Nationality = Gender 0.341 0.033** 0.006***

Nationality = Soc/Geo Groupings <0.001*** 0.005*** <0.001***

Nationality = Natural Other 0.294 0.699 0.648

Gender = Soc/Geo Groupings <0.001*** <0.001*** <0.001***

Gender = Natural Other 0.134 0.64 0.297

Soc/Geo Groupings = Natural Other 0.080* 0.018** 0.002***

Role Types

First Mover = Second Mover 0.444 0.552 0.175

First Mover = Simultaneous Mover 0.617 0.639 0.589

First Mover = Allocator <0.001*** 0.004*** <0.001***

First Mover = Partner Chooser 0.309 0.17 0.831

Second Mover = Simultaneous Mover 0.329 0.399 0.579

Second Mover = Allocator <0.001*** 0.001*** <0.001***

Second Mover = Partner Chooser 0.129 0.082* 0.621

Simultaneous Mover = Allocator 0.004*** 0.011** <0.001***

Simultaneous Mover = Partner Chooser 0.636 0.434 0.902

Allocator = Partner Chooser 0.021** 0.064* <0.001***

Note: *** p<0.01, ** p<0.05, * p<0.1; LPMa is linear probability model run on full sample, Metareg is meta-regression run on sample for which effect sizes are available, LPMb is linear probability model run on same sample as Metareg.

29

our finding on ethnicity – although the coefficient’s sign is at least weakly

significant15.16

Result 2: The strength of discrimination depends upon the type of group identity

under investigation. It is stronger when identity is artificially induced in the

laboratory than when the subject pool is divided by ethnicity or nationality, and

higher still when participants are split into socially or geographically distinct

groups.

3.3 How does the level of discrimination depend upon the decision-making

context?

Inspection of the coefficients on role type dummies in LPMa and Metareg (Table 2a)

reveals discrimination is significantly stronger when the decision-maker is a third-

party allocator than when he or she is a dictator (the omitted category). Linear

restriction tests (Table 2b) also show the third-party allocator role is more likely to be

associated with discrimination than all the other role types, with the difference always

significant at the 1% level under both models. The size of the Allocator coefficients in

the meta-regression (1.077) is worth noting – it indicates that discrimination in games

of this type tends to be very large indeed, with on average more than one standard

deviation between subjects’ treatment of in- and out-groups.

15 In Table 3, we will later present a meta-regression with the number of role type dummies reduced

from five to one. The purpose of this model is to investigate taste-based and statistical

discrimination. However, it is worth noting that in this model with fewer independent variables,

the coefficient on Ethnicity is found to be significantly negative at the 5% level. This improves our

confidence that there is an effect. The coefficient on Nationality is also significant (at the 1% level)

in that model.

16 We are particularly interested in the finding that discrimination is stronger in artificial group

experiments than those employing certain types of natural identity. In an attempt to gain a greater

understanding of what drives discrimination between artificial groups, we ran regressions focusing

on just the artificial identity sample, coding for the method experimenters used to create artificial

groups. We find it makes no difference whether groups are based on preferences (such as for a

particular painting) or sheer randomisation. Furthermore, we do not find that team-building

exercises designed to strengthen artificial group identity significantly increase the level of

discrimination. These results are all presented in greater detail in Appendix B.

30

The other role types do not carry significantly different effects from one

another. This is at odds with Kiyonari and Yamagishi (2004), and Balliet et al (2014),

who find discrimination to be stronger by simultaneous movers than first movers

(Balliet et al do not investigate second movers). In an attempt to discern why our

result differs from that of Balliet et al, we re-ran our analysis keeping only the

observations included in their study. We found there was still no significant difference

between First Mover and Simultaneous Mover (the remaining sample on which to run

this regression was small; however, we also compared the aggregate effect sizes for

each category and found they are very similar). This suggests the significance of the

finding in Balliet et al is driven by studies outside our dataset, i.e. outside the

economics literature.17

Result 3: Third-party allocators discriminate more than decision-makers in all

other roles.

3.4 Do students discriminate any more or less than non-students?

Most decision-makers in our analysis were students. Only 101 observations, from 22

studies, are produced by in-groups not comprised (at least in their near-entirely) of

university students. 31.8% of the observations for students return discrimination,

while 6.8% find out-group favouritism and 61.5% are null; for non-students 35.6%

find discrimination, 5.0% yield out-group favouritism and 59.4% are null. The

coefficient on Students is not significant in any of our regressions. That experiments

with students do not generate significantly different levels of discrimination than

those with non-students is an interesting non-result which suggests that, in this

literature, working with student samples will not generate a biased perception of the

extent and magnitude of discrimination by the wider population.18

17 With out-group favouritism as the dependent variable (LPMa1 in Appendix C, Table C.1), we find no

significant differences at all between any role type pair.

18 In Appendix B, we also show that the country where an experiment is run is not a significant

predictor of the extent of the discrimination found.

31

Result 4: Discrimination does not significantly differ between students and non-

students.

3.5 Does the experimental literature provide more support for taste-based or

statistical theories of discrimination?

For 262 (59.4%) of our observations, as a result of the experimental design any

discrimination must be taste-based, as it cannot be statistical. Statistical

discrimination cannot occur when a player is making the only or last move in a game,

unless the game is to be repeated, or possibly if the move is made simultaneously

with others. Discrimination by trust game returners, for example, can only be taste-

based, because opponents then have no control over the final outcome and beliefs

about their type are therefore irrelevant.19 All observations under the Dictator and

Allocator categories preclude the possibility of statistical discrimination, as do all

except seven (due to the game being repeated) in the Second Mover category. All

observations under the First Mover category permit the possibility of statistical

discrimination, as do most in the Partner Chooser category and around a third in the

Simultaneous Mover category.20

In Table 3, we run a linear probability regression on discrimination and a

meta-regression on the discrimination effect size, with role types re-coded into two

types: one, Taste + Statistical, where there is scope for both taste-based and statistical

discrimination, the other (the omitted category) where there is scope only for taste-

based discrimination. Note that in this literature any game-role contains scope for

taste-based discrimination. The coefficient on Taste + Statistical is positive but

insignificant in both the linear probability regression (p=0.87) and the meta-

regression (p=0.18). This indicates there is no significant difference in the likelihood

19 There is a grey area to be acknowledged here. One could have a model of statistical taste-based

discrimination, in which people have a taste for discrimination against a group because of beliefs

they hold about its members (for instance, about how rich they are). In this paper, we do not

distinguish between this and any other type of taste-based discrimination (i.e. we do not consider

root motivations for taste-based discrimination).

20 In Appendix A, Table A.2, we list which specific games permit which forms of discrimination.

32

of observing discrimination, or in the predicted effect size, when scope for statistical

discrimination is added.21

This would suggest taste-based discrimination is an important driver of

behaviour in these experiments and statistical discrimination is not, but we probe

further by analysing the results of individual experiments. Where there is scope for

statistically-motivated discrimination, by design for 66.5% of these observations it is

not possible to disentangle its effects from taste-based motivations. To be able to do

so, an experiment must either use belief elicitation or include a control game in which

behaviour can only be taste-based – the most common case of this is adding a dictator

game to extricate taste-based from statistical discrimination by trust game senders22.

In the 60 cases that it

21 We also ran a linear probability model on out-group favouritism, with the equivalent specification

to LPMa1 in Table 3. This is reported as LPMa2 in Appendix C, Table C.1. As with discrimination,

there is no significant difference in the likelihood of observing out-group favouritism when scope

for statistical discrimination is added.

22 There are no precisely standard methods for disentangling taste-based and statistical

discrimination. When using a control game in which only taste-based discrimination is possible,

statistical discrimination is identified if this game finds significantly weaker discrimination than the

setting with scope for both types of discrimination. When using belief elicitation, statistical

discrimination is confirmed if beliefs about the in-group and out-group significantly differ, and

there is significant discrimination in the direction that would maximise the decision-makers’

payoffs based on these beliefs; taste-based discrimination is confirmed if there is still significant

discrimination after controlling for the beliefs. Some studies use regression analysis, others non-

parametric tests.

33

Table 3: Linear probability regressions on discrimination and out-group

favouritism, and meta-regression on effect size, with or without scope for

statistical discrimination.23

Dependent variable Discrimination D

LPMa Metareg

Type of discrimination possible

Taste + Statistical 0.009 0.071

(0.056) (0.053)

Identity

Ethnicity -0.285*** -0.189**

(0.063) (0.080)

Religion -0.279** -0.232*

(0.134) (0.131)

Nationality -0.237*** -0.225***

(0.072) (0.079)

Gender -0.315*** -0.545***

(0.064) (0.100)

Soc/Geo Groupings 0.238** 0.265***

(0.097) (0.093)

Natural Other 0.074 -0.306

(0.266) (0.202)

Controls

Students 0.043 0.116

(0.072) (0.080)

Sample Size 4.5e-4 -2.7e-4

(4.7e-3) (4.4e-3)

Constant 0.350*** 0.238**

(0.089) (0.093)

R2 (adjusted in Metareg) 0.157 0.138 (adjusted)

N 441 364

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa is linear probability model run on full sample, Metareg is meta-regression run on sample for which effect sizes are available; omitted categories are taste-based only (type of discrimination possible) and Artificial (identity); errors in LPMa are corrected for heteroskedasticity, with 77 clusters; standard errors in parentheses.

23 Table 3 does not present an LPMb model because in this case we are not interested in

investigating any disparities between LPMa and Metareg – the Taste + Statistical coefficient is

insignificant in both models.

34

is possible to distinguish between discriminatory motives, the authors find significant

statistical discrimination to occur in 13 cases (10 times against the out-group and

three times in favour of it). Within the same sample, for given beliefs or behaviour in

a game with a belief-based component, they find significant taste-based deviations

from own-payoff-maximisation in 26 cases (16 times against the out-group and 10

times in favour of it). In 26 cases neither statistical nor taste-based discrimination is

found at the 5% level. We list all significant findings of taste-based and statistical

discrimination from experiments designed to distinguish between the two in

Appendix A, Table A.3.

Although the sample is small, tastes are found to affect behaviour more often

than statistical beliefs. It seems, however, that beliefs do play some role in

determining discriminatory behaviour in economics experiments. We conjecture that

the insignificant regression results in Table 3 may be due to the fact that beliefs can

either increase or reduce discrimination. This would be because individuals have

favourable beliefs about the cooperativeness of out-groups, or because unfavourable

beliefs about the out-group’s cooperativeness can in some cases actually lead to

statistical out-group favouritism. That is, depending on the game setting, self-serving

optimal behaviour can either become more or less generous in response to the

perception that one's partner is relatively uncooperative. In ultimatum games, for

instance, if proposers expect out-group responders to treat them less favourably than

in-group responders do, the self-serving optimum is to send them relatively kind

offers. This is in contrast to how first mover behaviour would work in trust games,

say, where a self-serving sender will send relatively low investments to an out-group

responder if it expects to be treated unfavourably by them.2425

24 We are unable to explore this empirically. We can separate games into those where favourable

beliefs about a partner’s cooperativeness should either increase or decrease the selfish decision-

maker’s cooperation towards them, but we would need data on beliefs about in-groups and out-

groups to predict the direction of discrimination this should result in.

25 In Appendix B, section B.4, we analyse how the relative strength of discrimination in experiments

featuring different identity types interacts with the type of discrimination possible. We show

discrimination is only significantly stronger across artificial groups than across ethnic, religious or

national groups when there is no scope for statistical discrimination, while discrimination is only

35

Result 5: There is evidence for both taste-based and statistical discrimination.

Tastes appear to drive the general tendency for discrimination against the out-

group, but individual studies have found beliefs to affect discrimination.

3.6 In gender experiments, how does male-to-female discrimination compare

with female-to-male discrimination?

An immediately obvious finding is that gender acts very differently from other

identity types. It is the only identity category which is more likely to be associated

with a bias against the in-group than against the out-group, with eight results of the

former and three of the latter out of a total 32 observations. On the reduced sample,

the random effects meta-analysis finds an overall discrimination effect size of -0.177

(95% confidence range: -0.301 – -0.053) for gender experiments, representing

significant out-group favouritism. There is obvious intuition why gender is different

from the other identity categories: it is the only case in which the effects of sexual

attraction – towards the out-group more than the in-group, for most subjects – and

‘chivalry’ (Eckel and Grossman, 2001) can be expected.

Every experiment on gender in the meta-analysis has a symmetrical male-

female design, meaning that for every estimate of discrimination by men against

women there is an identical treatment measuring discrimination by women against

men. This allows a very clean comparison of these two behaviours across the sample.

The only three significant results in our dataset of one gender discriminating against

the other are female decision-makers discriminating against males, while six of the

eight significant results of one gender favouring the other are male decision-makers

favouring females. However, the calculated overall effect size for female decision-

makers is actually slightly more negative than for males: -0.181 (95% confidence

range: -0.35 - -0.013) for females and -0.173 (95% confidence range: -0.369 – 0.024)

for males, although the difference is far from significant. Note that while the effect

significantly stronger across social/geographical groups than across artificial groups when there is

scope for statistical discrimination.

36

size indicates females significantly favour males at the 5% level, the equivalent effect

for male decision-makers is only significant at the 10% level.

Result 6: There is significant out-group favouritism in gender experiments.

Females significantly favour males; males favour females but the effect is only

weakly significant.

4. Discussion and Conclusions

A leading result of this paper is that discrimination in economics experiments varies

by the type of identity groups are based upon. It is very strong when groups are

socially or geographically distinct, and is relatively weak when they are based on

ethnicity or nationality. Notably, it tends to be relatively strong in experiments using

artificially-induced group identities – so it can confidently be stated that minimal

groups do not produce the minimal level of discrimination. At first glance, this seems

surprising.

It might be that artificial group manipulations are stronger priming

instruments than natural identity experiments tend to use – after all, these dedicate an

entire preliminary phase of the experiment to inducing feelings of identity, which will

remain at the front of subjects’ minds when they are then offered the chance to

discriminate. This explanation is arguably supported by the evidence of Robbins and

Krueger (2005), whose meta-analysis of psychology experiments shows subjects

exhibit stronger in-group projection – that is, they perceive in-group members to be

particularly similar to them, relative to out-group members – when identities are

artificial than when they are natural. On the other hand, we do not find that team-

building exercises, which are designed specifically to strengthen artificially-induced

identity and would seem to amplify priming, have a significant effect on the level of

discrimination (this is consistent with the findings of Chen and Li, 2009).

Conversely, it could be argued that, for the populations studied in the

literature, membership of particular ethnic and national groups does not actually instil

strong identity, so that even such trivial identities as can be artificially induced have a

greater effect. There is evidence that the process of globalisation has weakened

37

national and ethnic parochialism (Buchan et al, 2009), and in recent decades youth

identity in the West and increasingly elsewhere has come to define itself to a large

extent upon individuals’ belonging to subcultures based on fashion and music tastes –

preferences drawn from choice sets which are not, indeed, so different from the

apparently arbitrary minimal group painting dichotomy. However, it would seem

highly complacent to draw the conclusion from our results that racism and

xenophobia are not big problems in many societies.

Another explanation may be that subjects in ethnic and national identity

experiments are shying away from displaying ‘politically incorrect’26 behaviour,

given that racism and xenophobia are taboo in most societies today. While the link

between social acceptability and discrimination has not been well explored, the

prejudice literature has yielded relevant findings: that expressions of prejudice

correlate with perceptions towards the social acceptability of such prejudice (e.g.

Crandall et al, 2003), and furthermore that this correlation is at least partly the result

of norm-compliance (e.g. Blanchard et al, 1994).

It seems unlikely that discriminating on the basis of a stated preference for

Klee’s paintings over Kandinsky’s carries any taboo similar to ethnic or national

discrimination. Indeed, some subjects may regard an artificial group situation as a

game in which they belong to one of the teams, wherein the social norm actively

encourages favouritism of one’s own group – the sheer strangeness of the setting may

even lead subjects to perceive a demand for discrimination on the part of the

experimenter (see e.g. Zizzo, 2010). Concerns about social acceptability could

explain also why the Soc/Geo Groupings category produces significantly higher

discrimination than other types of natural identity. Of course, it would not be

surprising if relational and geographic proximity led to a stronger sense of belonging

26 Political correctness is defined as ‘The avoidance of forms of expression or action that are

perceived to exclude, marginalize, or insult groups of people who are socially disadvantaged or

discriminated against’ (Oxford Dictionaries).

38

than shared ethnicity, religion or nationality, but bear in mind too that there is

arguably no taboo against favouring friends over strangers27.

If it were shown that discrimination in economics experiments is indeed

limited by concerns about social acceptability, it might cast doubt over the external

applicability of such studies’ findings. It is possible that if participants guess an

experiment is about a type of discrimination which is taboo, it will systematically

generate a lower effect than if the subjects were unaware of its purpose. On the other

hand, the very same concerns about social acceptability might also limit certain types

of discrimination outside the lab.

It is noteworthy that gender is the identity category producing the weakest

discrimination: in fact, here the meta-analysis finds a significant amount of out-group

favouritism. However, gender discrimination clearly persists in the outside world. It

may be that economics experiments do not find it because they poorly reflect the

conditions under which it survives beyond the lab – in particular, in the job market.

It would be interesting to see more experiments designed to directly compare

the effects of different types of group identity. This meta-analysis includes just four.

Dugar and Shahriar (2009), Li et al (2011) and Goette et al (2012) all compare

discrimination between social/geographical groups and artificial groups, while

Abbink and Harris (2012) use artificial groups and political groups (which fall under

the Natural Other category). The results of all four studies are consistent with ours –

discrimination is always lower with artificial identity. However, direct comparisons

between artificial group and ethnic or national discrimination are lacking, and it

would be very illuminating to see whether such studies support – and if so, whether

they can explain – the findings of this meta-analysis.

What implications does our research have for future experiments on

discrimination? First, using artificially induced identities as a control against which to

pit the results of natural identity treatments may not be recommendable, as the

27 This does depend upon the context, however. There are strong taboos against nepotism in certain

labour-market transactions. Possibly, the experiments in this literature do not recreate such

circumstances.

39

artificial group manipulation appears not so much to capture the minimal level of

discrimination that must result from priming any type of identity in a laboratory as to

in fact often go beyond that.

Regarding role type, we find discrimination by third-party allocators is much

stronger than by participants in any other game setting. If social acceptability does

indeed limit discrimination, this is a counterintuitive result, as the allocator role

essentially invites subjects to overtly and consciously favour one group over another

and therefore seems to be the one that most obviously telegraphs the purpose of this

type of experiment. One possibility is that the role carries an experimenter demand

effect – whereby subjects feel they are encouraged to discriminate – or even an action

bias effect, if the equal split feels like a default non-move. Another relevant factor

may be that the third-party allocator is unique amongst our role types in the decision-

maker’s payoff being entirely disconnected from the extent to which they

discriminate. In any case, experimenters should bear in mind that because they are

more likely to identify significant discrimination when they employ the allocator role,

they should be less confident that the same groups will discriminate against each

other in different contexts.

We find the strength of discrimination does not significantly differ between

student and non-student subject pools. This suggests – unlike in the context of social

preferences (e.g. Bellemare and Kroger, 2007; Anderson et al, 2013) – student

subjects are not a generally unrepresentative sample for questions relating to

discrimination. However, we do not exclude the possibility that they are

unrepresentative in specific instances, or within particular societies.

There is scope for more experimental research investigating taste-based and

statistical discrimination. We show both are relevant, and the two types manifest

themselves to different extents in different contexts. However, relatively few

experiments have been designed to distinguish between taste-based and statistical

discrimination, and more could be known about the mechanisms underlying them.

As a final observation, there is a great deal of variation in the findings of the

experimental economics discrimination literature. Our analysis can explain some of it,

but our LPM regressions typically have R2 statistics below 0.2, and the meta-

40

regressions’ Adjusted R2s are rarely above 0.35. As might be expected, discrimination

does seem to vary idiosyncratically and is not easy to predict. The results of natural

identity experiments do not seem very generalizable – they probably reflect more the

characteristics of the specific groups under investigation, and the relationships

between them, than aspects of the experimental design. Whilst a drawback for some

research questions, this also means there is a great deal of scope for future

experimental studies aimed at measuring the levels of discrimination within subject

pools of specific interest. Furthermore, given the potential concerns we raise about

experimenter demand effects and the external validity of lab experiments on

discrimination, the important role of field experiments should be emphasised.

Subjects in such studies are unaware they are being observed by experimenters and

their behaviour can therefore not be influenced by the fact. Field experiments can test

the generalisability of lab findings on discrimination.

Acknowledgements

Many thanks to Abigail Barr and Daniele Nosenzo for their support and input. I am

very grateful to all authors who sent data for this project. I received helpful comments

at presentations in Nottingham, Duisburg and Warwick from, amongst others, Swee-

Hoon Chuah, Simon Gächter, Gianluca Grimalda, Heike Hennig-Schmidt and Gari

Walkowitz. Thanks to the Network for Integrated Behavioural Science for financial

support.

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51

Appendix A

Table A.1: Subjective decisions on appropriately defined groups

Study Notes

Burns, 2004 We consider ‘coloured’ to be an appropriate ethnic

group in South Africa (as defined in comparison to

‘white’ and ‘black’).

Chen et al, 2011 We do not consider ‘Asian’ to be an appropriate ethnic

group in the USA.

Ferraro and Cummings, 2007 We consider ‘Hispanic’ to be an appropriate ethnic

group in the USA. (Justification, relative to ‘Asian’:

Hispanic people in the USA share a more unified culture

than those of Asian descent; they are descended from

more linguistically homogeneous peoples than Asians)

Friesen et al, 2012 We do not consider ‘East Asian’ and ‘South Asian’ to be

appropriate ethnic groups in Canada.

52

Table A.2: Game types in meta-analysis and how they measure discrimination

Role Type How discrimination is measured Type of discrimination possible

Trust Game Returner

Difference in proportion of amount received from the sender that is returned*, between in-group and out-group matching. *NB: Ploner and Soraperra (2004) use Indirect Trust Game, where the amount returned is not given to the sender but a group member of theirs

Taste-based only

Agent in Principal-Agent Game (Masella et al, 2012)

Difference in amount sent to principal, between in-group and out-group matching.

Taste-based only

Dictator; Proposer in Unilateral Power Game (Zizzo, 2011)

Difference in amount sent to recipient, between in-group and out-group matching. (NB: Buchner and Dittrich (2002) use a saving game where one player leaves the game early and decides how much to leave their partner. This decision is the equivalent of that faced by a dictator)

Taste-based only

Allocator Difference in amount allocated to in-group and out-group member.

Taste-based only

Responder in Ultimatum Game, Hold-up Game (Morita and Servatka, 2013)

Difference in likelihood of rejecting an offer, controlling for its size, between in-group and out-group matching.

Taste-based only

Responder in Proposer-Responder Game (McLeish and Oxoby, 2007)

Difference in amount by which proposer’s payoff is reduced, controlling for amount offered by proposer, between in-group and out-group matching.

Taste-based only

Responder in Proposer-Responder Game (Chen and Li, 2009; Currarini and Mengel, 2012)

Difference in rate of choosing more other-regarding response, between in-group and out-group matching.

Taste-based only

Third-party punisher Difference in punishment level, controlling for behaviour of punishee, between in-group and out-group matching.

Taste-based only

One-shot Prisoner’s Dilemma

Difference in rate of cooperation, between in-group and out-group matching.

Taste-based only

Trader in market games

For bidders: difference in price offered, between in-group and out-group matching. For sellers: difference in price accepted, between in-group and out-group matching.

Taste-based only for sellers in one-shot interactions; taste-based and statistical for bidders in one-shot interactions, and for all players in repeated games.

Public Goods Game Difference in contribution level, between in-group and out-group matching.

Taste-based only in one-shot games (Hopfensitz, 2013);

53

taste-based and statistical in repeated games.

Partner-Choosing Role

Difference in rate of choosing in-group partner and out-group partner.

Taste-based only if chosen partner does not become active decision-maker in subsequent games; taste-based and statistical if they do.

Repeated Common Pool Withdrawal Game (Carpenter and Cardenas, 2011)

Difference in withdrawal level, between in-group and out-group matching.

Taste-based and statistical.

Minimal Effort Game (Chen and Chen, 2011)

Difference in effort level, between in-group and out-group matching.

Taste-based and statistical.

Trust Game Sender; Principal in Principal-Agent Game (Masella et al, 2012); First Mover in Hold-up Game (Morita and Servatka, 2013)

With continuous action space: difference in amount sent, between in-group and out-group matching. With binary action space: difference in rate of choosing to trust, between in-group and out-group matching.

Taste-based and statistical.

Investor in Investment Game (Wu, 2009)

Difference in amount invested in manager’s project, between in-group and out-group matching.

Taste-based and statistical.

Ultimatum Game Proposer; Second Mover in Hold-up Game (Morita and Servatka, 2013); First Mover in Proposer-Responder Game (McLeish and Oxoby, 2007)

Difference in amount offered, between in-group and out-group matching.

Taste-based and statistical.

Proposer in Proposer-Responder Game (Chen and Li, 2009; Currarini and Mengel, 2012)

Difference in rate of choosing more other-regarding first move, between in-group and out-group matching.

Taste-based and statistical.

Nash Demand Game (Ruffle and Sosis, 2006; Zizzo, 2011)

Difference in amount claimed, between in-group and out-group matching

Taste-based and statistical.

Stag Hunt Difference in rate of choosing hawkish strategy, between in-group and out-group matching.

Taste-based and statistical.

54

Table A.3: List of significant results from studies designed to distinguish

between taste-based and statistical discrimination

Result Paper Role Groups

Taste-based and statistical discrimination

Banuri et al (2012) Partner-choosing role Colleges within university (Free Nepotism treatment)

Bernhard et al (2006) Dictator Tribes

Binzel and Fehr (2013) Trust Game Sender Social groups

Currarini and Mengel (2012)

Partner-choosing role Artificial (comparison of COORD, ENDO and LOWB treatments)

Etang et al (2011a) Trust Game Sender Villages

Taste-based discrimination only

Burns (2004) Trust Game Sender Ethnic (coloured in-group, black out-group)

Trust Game Sender Ethnic (coloured in-group, white out-group)

Chuah et al (2013) Trust Game Sender Religious (Hindu in-group, Muslim out-group)

Trust Game Sender Religious (Muslim in-group, Hindu out-group)

Ferraro and Cummings (2007)

Ultimatum Game Proposer Ethnic (Hispanic in-group, Navajo out-group)

Guillen and Ji (2011) Trust Game Sender National (Australian in-group, non-Australian out-group)

Kim et al (2013) Trust Game Sender

National (North Korean in-group, South Korean out-group – sample 1)

Trust Game Sender National (North Korean in-group, South Korean out-group – sample 2)

McLeish and Oxoby (2007)

First Mover in Proposer-Responder Game

Artificial (OP treatment)

First Mover in Proposer-Responder Game

Artificial (NO treatment)

Ruffle and Sosis (2006) Nash Demand Game Social/geographical (Kibbutz in-group, city out-group)

Statistical discrimination only

Banuri et al (2012) Partner-choosing role Colleges within university (Costly Nepotism treatment)

Boarini et al (2009) Ultimatum Game Proposer National (French in-group, Indian out-group)

Chen and Chen (2011) Minimal Effort Game Artificial (Enhanced treatment)

Haile et al (2008) Trust Game Sender Ethnic (white in-group, black out-group)

Masella et al (2014) Principal in Principal-Agent Game

Artificial

Taste-based out-group favouritism only

Burns (2004)

Trust Game Sender Ethnic (white in-group, black out-group)

Trust Game Sender Ethnic (black in-group, white out-group)

Trust Game Sender Ethnic (black in-group, coloured out-group)

Hennig-Schmidt et al (2007)

Trust Game Sender National (Israeli in-group, Palestinian out-group)

Trust Game Sender National (Palestinian in-group, Israeli out-group)

Kim et al (2013)

Trust Game Sender National (South Korean in-group, North Korean out-group – sample 1)

Trust Game Sender National (South Korean in-group, North Korean out-group – sample 2)

Slonim and Guillen (2010)

Trust Game Sender Gender (male in-group, Gender/Ability Selection treatment)

Trust Game Sender Gender (male in-group, No Selection treatment)

Partner-choosing role Gender (male in-group, Trust Game treatment)

Statistical out-group favouritism only

Boarini et al (2009) Ultimatum Game Proposer National (Indian in-group, French out-group)

Hennig-Schmidt et al (2007)

Trust Game Sender National (German in-group, Palestinian out-group)

Slonim and Guillen (2010)

Partner-choosing role Gender (female in-group, Trust Game treatment)

55

Appendix B: Further Results

B.1 Further analysis of role types

In this section we investigate the effects on discrimination of using specific game

types. We recode the role type variables, assigning dummies to specific game settings

in the following way. Trust games and similar principal-agent games provide two

roles: senders (TG Sender, 98 observations) and returners (TG Returner, 81). The next

most common role type is the Dictator (68). Prisoner’s dilemmas, public goods

games, and common pool withdrawal games are all social dilemmas, and are coded

under a single category (Social Dilemma, 58). Next we have third-party allocators

(Allocator, 33). Ultimatum games and similar bargaining settings are grouped

together and split into two role types: first movers (Proposer, 31) and second movers

(Responder, 27). Treating Dictator as the omitted category in our regressions, we

form a set of binary independent variables from the other six role types, plus the

additional variable Game Other (45 observations) into which are placed the

remaining game settings that we did not think could be adequately categorised.28

Table C.3a in Appendix C displays the output of regressions incorporating

these variables. These regressions are the equivalent of those presented in Table 2, the

only change being the recoding of the role type variables. As above, LPMa1 and

Metareg1 show discrimination to be significantly stronger when the decision-maker is

a third-party allocator than when he or she is a dictator (the omitted category). Linear

restriction tests (Table C.3b) also show the third-party allocator role is more likely to

be associated with discrimination than all the other role types, with the difference

always significant at the 1% level under both models. Again, the other role types do

not consistently carry significantly different effects from one another. This is at odds

with the analysis of Balliet et al (2014), who find discrimination is stronger by trust

28 Specifically, the Game Other category consists of players in the following settings: unstructured

bargaining games; the battle of the sexes; coordination games; indirect trust games; market-

trading games; minimal effort games; Nash Demand games; partner-choosing situations; saving

games; stag hunts; and third-party punishment games. Several of these could have been coded

under a standalone category – coordination games and variants – but there would only be eight

observations in such a category.

56

game senders than by dictators, and stronger still in social dilemmas. With out-group

favouritism as the dependent variable (LPMa2), the only significant differences

between role types are that proposers are less likely to engage in out-group

favouritism than dictators, trust game senders, trust game returners and subjects in the

Game Other category.

Result A1: We do not find strong effects associated with such specific role types as

the trust game sender or returner, players in social dilemmas, or bargaining game

proposers or responders.

B.2 Does the strength of discrimination in artificial group experiments depend

on the method used to induce identity?

The way in which identity is artificially instilled in subjects varies from experiment to

experiment. However, we can identity two broad categories of artificial group

creation. One follows the original Tajfel et al (1971) process of allowing subjects to

self-select into groups. Typically this involves asking participants to choose a

preference between the art of Klee and Kandinsky, although some studies elicit

preferences on other choice sets, such as favourite colours. We code these

observations under Preferences. The other main category gives subjects no control

over which group they belong to. In such cases they are simply randomly assigned

and labelled as belonging to, for instance, the ‘red’ or ‘blue’ group. We code these

manipulations as Labelling. Occasionally, a different type of identity inducement is

done – for example, groups can be based on subjects’ tendency to overestimate or

underestimate the number of dots on a screen (Guala et al, 2013; Ioannou et al, 2013),

or by the time at which they undertake a particular task (Ahmed, 2007). These cases

we code as Other Method.

Another way artificial group manipulations vary is by whether they contain

additional stages in which group members interact, between being placed into groups

and before the task upon which discrimination is measured. These stages often

involve games in which group members must work together to earn monetary

rewards, although on some occasions they merely interact non-strategically as a result

57

of being permitted to converse electronically. Such stages are introduced as a

mechanism to strengthen artificial group identities. We code their presence in studies

under Team Building.

In order to test how these different procedures affect the extent of

discrimination, we run LPM and meta-regressions on our sub-sample of observations

for which identity is artificial. These are presented in Appendix C, Table C.4. We find

there is no significant difference between whether groups are self-selected or

randomly selected. Also, while the coefficients are in the direction of strengthening

discrimination, we find the effect of team-building exercises not to be significant.

From these results, we infer that the precise form of identity inducement is not crucial

to the outcome of artificial group experiments. This is consistent with the findings of

Chen and Li (2009), whose experiment addresses these questions.

Result A2: The strength of discrimination in artificial group experiments does not

depend significantly on the method used to induce identity.

B.3 Can country-level variables explain discrimination?

Our meta-analysis encompasses geographical diversity, with data from 31 countries.

Including cases where the out-group was located in a different country, 169 results

from 34 studies come from Europe, 116 observations from 22 studies are from North

America, 85 results from 17 studies are from Asia, 37 observations from seven

studies come from Africa, nine results from three studies come from Latin America,

and ten observations from three studies are from Australasia. Ten results from two

papers have decision-makers located in more than one country, while one paper does

not mention where its experiment took place. The country providing the most

observations is the USA, with 106 from 19 studies.

This diversity allows us a further set of variables to test for relationships

between discrimination and characteristics of the country in which an experiment is

run. In Appendix C, Table C.5, therefore, we report regressions including location

dummies for the USA and Europe, and country-level measures of Individualism (from

the Hofstede Centre), ethno-linguistic-religious Fractionalisation (constructed from

58

Alesina et al, 2003, by averaging each country’s scores for ethnic, linguistic and

religious fractionalization29) and prosperity (Log GDPpc, the log of per capita

national income at purchasing power parity, as estimated by the World Bank). Using

these independent variables requires trimming the sample to exclude experiments

conducted across countries, as well as those in locations for which data on

Individualism is not available.

We do not find any country-level variables to be significant, with rare

exceptions. In LPMa2, we find the probability of observing out-group favouritism is

lower in the USA than in the rest of the world, significant at the 5% level. However,

once controlling for country-level individualism, as in LPMa3, the effect disappears.

Individualism itself only has a weakly significant effect of reducing the likelihood of

out-group favouritism, after omitting the USA dummy in LPMa4.

While the insignificance of country-level variables in our analysis appears to

show that results on discrimination can be generalised across cultures, we do not

argue this is necessarily the case. The locations at which experiments on

discrimination have been conducted are not a random global sample; in many cases

they are handpicked by researchers who have prior reason to believe they have an

interesting discrimination-related question to ask of a particular subject pool.

Result A3: Country-level variables are not found to significantly explain

discrimination.

B.4 How does the experimental context affect the prevalence of each type of

discrimination?

To investigate the strength of different types of discrimination in experiments with

different types of identity, we run LPM and meta-regressions on the sub-sample of

observations for which there is scope only for taste-based discrimination, and the sub-

sample for which there is scope for both taste-based and statistical discrimination.

29 We also ran regressions containing separate variables for ethnic, linguistic and religious

fractionalization, none of which were found to have significance.

59

The results are presented in Appendix C, Table C.6a; LPMa1 and Metareg1 relate to

the taste-based only sub-sample, while LPMa2 and Metareg2 relate to the both-types

sub-sample. The table reports whether the coefficients for each identity category

significantly differ between models 1 and 2; this is deduced by running pooled

models with interaction terms. The results of linear restriction tests are also presented

in Appendix C, Table C.6b.

When it can only be driven by taste, according to both the LPM and the meta-

regression discrimination is significantly greater across artificial groups than across

ethnicities, religions, nationalities or gender. All of these differences are significant at

the 1% level, apart from the difference between Artificial and Religion in Metareg(1),

which is significant at the 5% level. However, when discrimination can be driven

both by tastes and statistical beliefs, neither model finds it to significantly differ

between artificial group experiments and those on nationality, religion or ethnicity.30

With only taste-based discrimination possible, discrimination is not

significantly different across artificial groups to across socially or geographically

distinct groups. However, when there is also scope for statistical discrimination,

discrimination is significantly higher (1% level) among socially or geographically

distinct groups.

The only identity category whose coefficient significantly differs between the

sample where only taste-based discrimination is possible and the sample where both

types of discrimination are possible, in models ran on both dependent variables, is

Soc/Geo Groupings. The coefficients on Ethnicity, Religion and Nationality do not

significantly differ between samples. The test on the omitted category, Artificial,

shows its coefficient also does not significantly differ between samples. We therefore

interpret the narrowing of the discrimination gap between Artificial and Ethnicity,

Religion and Nationality when scope is added for statistical discrimination as being

driven by beliefs either reducing discrimination in artificial identity experiments, or

enhancing it in experiments with ethnicity, religion and nationality, or both. We

interpret the widening of the discrimination gap between Artificial and Soc/Geo

30 Except with Ethnicity at the 10% level in the LPM.

60

Groupings when scope is added for statistical discrimination as being driven

primarily by beliefs enhancing discrimination between social and geographical

groups.

Result A4: Discrimination is only significantly stronger between artificial groups

compared to between ethnic, religious and national groups when there is scope only

for taste-based discrimination. Discrimination is only significantly stronger

between social/geographical groups compared to between artificial groups when

there is scope for both types of discrimination.

61

Appendix C: Additional Regression Output

Table C.1: Linear probability regressions on out-group favouritism

Dependent variable Out-group favouritism

LPMa1 LPMa2

Type of discrimination possible

Taste + Statistical -0.003

(0.020)

Role Types

First Mover -0.031

(0.029)

Second Mover -0.012

(0.027)

Simultaneous Mover -0.025

(0.038)

Allocator -0.049

(0.037)

Partner Chooser 0.031

(0.063)

Identity

Ethnicity 0.041 0.035

(0.040) (0.036)

Religion -0.004 -0.008

(0.052) (0.050)

Nationality 0.118* 0.111

(0.069) (0.068)

Gender 0.222*** 0.231***

(0.046) (0.047)

Soc/Geo Groupings -0.051** -0.045*

(0.024) (0.023)

Natural Other -0.025 -0.041

(0.034) (0.026)

Controls

Students -0.023 -0.026

(0.041) (0.038)

Sample Size 4.9e-4 2.0e-4

(7.2e-4) (2.9e-4)

Constant 0.051 0.038

(0.046) (0.047)

R2 0.088 0.084

N 441 441

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa1 and LPMa2 are linear probability models run on full sample; omitted categories are Dictator (role type) and Artificial (identity); errors are corrected for heteroskedasticity, with 77 clusters; standard errors in italics.

62

Table C.2: Logistic regressions on discrimination and out-group favouritism

Dependent variable Discrimination Out-group favouritism

LOGITa1 LOGITa2

Identity

Ethnicity -0.260*** 0.062

(0.046) (0.069)

Religion -0.195** -0.003

(0.098) (0.061)

Nationality 0.216*** 0.172*

(0.065) (0.095)

Gender -0.252*** 0.326***

(0.045) (0.097)

Soc/Geo Groupings 0.244** (dropped)

(0.111)

Natural Other -0.056 (dropped)

(0.138)

Role Types

First Mover -0.031 -0.022

(0.081) (0.017)

Second Mover -0.080 -0.007

(0.066) (0.017)

Simultaneous Mover 0.025 -0.011

(0.113) (0.030)

Allocator 0.413*** -0.035**

(0.103) (0.014)

Partner Chooser 0.075 0.035

(0.125) (0.045)

Controls

Students 0.011 -0.037

(0.072) (0.053)

Sample Size 1.7e-4 1.9e-4

(4.9e-4) (1.8e-4)

Pseudo R2 0.167 0.132

N 441 367

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa1 and LPMa2 are linear probability models run on full sample; omitted categories are Dictator (role type) and Artificial (identity); errors are corrected for heteroskedasticity, with 77 clusters in LOGITa1 and 66 in LOGITa2; standard errors in parentheses; for dummy variables, dy/dx is for discrete change from 0 to 1.

63

Table C.3a: Linear probability regression on discrimination and meta-regression

on effect size (further analysis of role type)

Dependent variable Discrimination d Out-group favouritism

LPMa1 LPMb1 Metareg1 LPMa2

Identity

Ethnicity -0.287*** -0.282*** -0.113 0.032

(0.078) (0.084) (0.081) (0.041)

Religion -0.219 -0.220 -0.092 -0.027

(0.141) (0.156) (0.128) (0.057)

Nationality -0.234*** -0.133 -0.112 0.107

(0.085) (0.106) (0.078) (0.067)

Gender -0.314*** -0.339*** -0.500*** 0.233***

(0.065) (0.069) (0.098) (0.042)

Soc/Geo Groupings 0.242** 0.242* 0.365*** -0.057**

(0.102) (0.124) (0.091) (0.023)

Natural Other -0.069 -0.286 -0.203 -0.034

(0.176) (0.179) (0.193) (0.035)

Role Types

TG Sender -0.045 -0.045 0.002 -2.6e-4

(0.126) (0.086) (0.081) (0.027)

TG Returner -0.126* -0.147* -0.112 0.016

(0.074) (0.083) (0.087) (0.024)

Social Dilemma 0.014 0.010 -0.022 -0.011

(0.106) (0.115) (0.097) (0.039)

Allocator 0.348*** 0.400*** 0.991*** -0.042

(0.104) (0.141) (0.154) (0.034)

Proposer -0.081 -0.131 -0.012 -0.088**

(0.101) (0.090) (0.106) (0.041)

Responder -0.029 0.129 0.120 -0.017

(0.099) (0.109) (0.135) (0.055)

Game Other 0.045 0.087 0.034 0.004

(0.098) (0.119) (0.104) (0.037)

Controls

Students 0.004 -0.028 0.103 -0.018

(0.068) (0.077) (0.077) (0.040)

Sample Size 1.2e-4 5.7e-5 -7.1e-4* 2.7e-4

(4.3e-4) (4.7e-3) (4.3e-3) (3.2e-3)

Constant 0.416*** 0.442*** 0.236** 0.037

(0.087) (0.100) (0.106) (0.048)

R2 (adjusted in Metareg1) 0.206 0.214 0.237 0.094

N 441 364 364 441

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa1 and LPMa2 are linear probability models run on full sample, Metareg1 is meta-regression run on sample for which effect sizes are available, LPMb1 is linear probability model run on same sample as Metareg1; omitted categories are Dictator (role type) and Artificial (identity); errors in LPM models are corrected for heteroskedasticity, with 77 clusters in LPMa1 and LPMa2, and 67 in LPMb1; standard errors in italics.

64

Table C.3b: Linear Restriction Tests on models presented in Table C.3a

Null Hypothesis

P Value on two-tailed test

LPMa1 LPMb1 Metareg1 LPMa2

Identity

Ethnicity = Religion 0.613 0.652 0.872 0.43

Ethnicity = Nationality 0.553 0.157 0.991 0.256

Ethnicity = Gender 0.705 0.452 0.001*** <0.001***

Ethnicity = Soc/Geo Groupings <0.001*** <0.001*** <0.001*** 0.066*

Ethnicity = Natural Other 0.203 0.983 0.642 0.164

Religion = Nationality 0.909 0.571 0.884 0.126

Religion = Gender 0.496 0.431 0.009*** <0.001***

Religion = Soc/Geo Groupings 0.001*** 0.002*** <0.001*** 0.544

Religion = Natural Other 0.47 0.735 0.586 0.902

Nationality = Gender 0.286 0.017** 0.001*** 0.085*

Nationality = Soc/Geo Groupings <0.001*** 0.007*** <0.001*** 0.017**

Nationality = Natural Other 0.374 0.424 0.653 0.017**

Gender = Soc/Geo Groupings <0.001*** <0.001*** <0.001*** <0.001***

Gender = Natural Other 0.169 0.769 0.16 <0.001***

Soc/Geo Groupings = Natural Other 0.092* 0.004*** 0.003*** 0.452

Role Types

TG Sender = TG Returner 0.25 0.171 0.119 0.53

TG Sender = Social Dilemma 0.605 0.648 0.782 0.808

TG Sender = Allocator <0.001*** 0.008*** <0.001*** 0.2

TG Sender = Proposer 0.709 0.343 0.887 0.030**

TG Sender = Responder 0.891 0.25 0.37 0.758

TG Sender = Game Other 0.381 0.282 0.748 0.907

TG Returner = Social Dilemma 0.206 0.176 0.31 0.526

TG Returner = Allocator <0.001*** 0.001*** <0.001*** 0.138

TG Returner = Proposer 0.647 0.863 0.341 0.016**

TG Returner = Responder 0.414 0.061* 0.085* 0.551

TG Returner = Game Other 0.086* 0.050* 0.155 0.758

Social Dilemma = Allocator 0.014*** 0.019** <0.001*** 0.398

Social Dilemma = Proposer 0.415 0.213 0.932 0.058*

Social Dilemma = Responder 0.761 0.458 0.309 0.912

Social Dilemma = Game Other 0.788 0.564 0.616 0.726

Allocator = Proposer <0.001*** <0.001*** <0.001*** 0.158

Allocator = Responder 0.005*** 0.107 <0.001*** 0.626

Allocator = Game Other 0.018** 0.050** <0.001*** 0.234

Proposer = Responder 0.722 0.093* 0.367 0.183

Proposer = Game Other 0.186 0.021** 0.699 0.034**

Responder = Game Other 0.542 0.806 0.554 0.699

Note: *** p<0.01, ** p<0.05, * p<0.1; LPMa is linear probability model run on full sample, Metareg is

meta-regression run on sample for which effect sizes are available, LPMb is linear probability model run on same sample as Metareg.

65

Table C.4 Linear probability regressions on discrimination and meta-regressions

on effect size for artificial identity experiments only

Dependent variable Discrimination d

LPM Metareg

Role Types

First Mover -0.190 -0.074

(0.165) (0.127)

Second Mover -0.102 -0.098

(0.142) (0.135)

Simultaneous Mover -0.211 -0.005

(0.154) (0.139)

Allocator 0.236* 0.898***

(0.130) (0.170)

Partner Chooser 0.061 0.083

(0.213) (0.182)

Controls

Students 0.032 0.128

(0.123) (0.207)

Sample Size 0.002*** 0.001

(0.001) (0.001)

Identity Inducement Method

Labelling -0.117 0.030

(0.081) (0.085)

Other Method -0.140 0.102

(0.125) (0.141)

Team Building 0.085 0.031

(0.095) (0.691)

Constant 0.409* 0.102

(0.207) (0.247)

R2 (adjusted for Metareg) 0.154 0.262

N 169 146

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPM is linear probability model run on artificial identity sample, Metareg is meta-regression run on artificial identity sample for which effect sizes are available; omitted categories are Dictator (role type) and Preferences (Identity inducement method); errors in LPM are corrected for heteroskedasticity, with 32 clusters; standard errors in parentheses.

66

Table C.5: Linear probability regressions on discrimination and out-

group favouritism, and meta-regression on effect size, with country-level

variables included

Dependent variable Discrimination d Out-group favouritism

LPMa1 Metareg1 LPMa2 LPMa3 LPMa4

Identity Ethnicity -0.220** -0.171 0.053 0.044 0.042 (0.086) (0.104) (0.045) (0.045) (0.042) Religion -0.146 -0.198 0.014 -0.063 -0.069 (0.192) (0.179) (0.040) (0.090) (0.079) Gender -0.294*** -0.386*** 0.254*** 0.244*** 0.239*** (0.100) (0.113) (0.047) (0.048) (0.045) Soc/Geo Groupings 0.260** 0.273*** -0.029* -0.052* -0.055** (0.103) (0.095) (0.016) (0.029) (0.025) Natural Other 0.008 -0.311 -0.023 -0.093 -0.099* (0.177) (0.213) (0.017) (0.068) (0.057) Role Types First Mover -0.027 0.245*** -0.013 -0.012 -0.012 (0.101) (0.088) (0.024) (0.025) (0.025) Second Mover -0.086 0.182* 0.014 0.014 0.014 (0.080) (0.094) (0.025) (0.026) (0.026) Simultaneous -0.080 0.206* -0.004 -0.004 -0.006 (0.108) (0.110) (0.027) (0.028) (0.029) Allocator 0.423*** 1.178*** -0.026 -0.046 -0.049* (0.142) (0.165) (0.020) (0.029) (0.027) Partner Chooser 0.058 0.208 0.049 0.067 -0.066 (0.130) (0.141) (0.060) (0.063) (0.063) Controls Fractionalisation 0.015 0.414 (0.265) (0.257) LogGDPpc 0.020 -0.031 (0.083) (0.089) Europe 0.100 0.277* (0.131) (0.150) USA 0.038 0.096 -0.049** -0.012 (0.132) (0.163) (0.022) (0.034) Individualism -0.001 -0.001 -0.002 -0.002* (0.004) (0.003) (0.002) (0.001) Constant 0.191 0.174 0.035* 0.167 0.179* (0.731) (0.813) (0.021) (0.119) (0.094) R2 (adjusted in Metareg1)

0.217 0.256 0.112 0.122 0.122

N 345 304 359 345 345 Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa1, LPMa3 and LPMa4 are linear probability models run on full sample excluding experiments conducted across countries and in countries for which data on Individualism is not available, LPMa2 is linear probability model run on full sample excluding experiments conducted across countries, Metareg1 is meta-regression run on sample for which effect sizes are available excluding experiments conducted across countries and in countries for which data on Individualism is not available; omitted categories are Dictator (role type) and Artificial (identity); errors in LPM models are corrected for heteroskedasticity, with 60 clusters in LPMa1, LPMa3 and LPMa4, and 65 in LPMa2; standard errors in parentheses.

67

Table C.6a: Linear probability regressions on discrimination and meta-

regressions on effect size, with scope only for taste-based discrimination (Model

1) and scope for both types of discrimination (Model 2)

Dependent variable Discrimination d

Taste-based only

Taste + Statistical

Test of coefficient difference

Taste-based only

Taste + Statistical

Test of coefficient difference LPMa1 LPMa2 Metareg1 Metareg2

Identity

Ethnicity -0.351*** -0.195* -0.291*** 0.020

(0.078) (0.100) (0.088) (0.169)

Religion -0.474*** -0.159 -0.443** -0.048

(0.125) (0.234) (0.172) (0.206)

Nationality -0.292*** -0.162 -0.312*** -0.133

(0.089) (0.122) (0.115) (0.113)

Gender -0.290*** -0.352*** -0.474*** -0.642***

(0.090) (0.080) (0.122) (0.167)

Soc/Geo Groupings 0.081 0.408*** ** 0.015 0.532*** ***

(0.159) (0.126) (0.125) (0.142)

Natural Other 0.146 -0.224 -0.301 -0.227

(0.263) (0.262) (0.329) (0.281)

Controls

Students 0.041 -0.047 0.034 0.178

(0.101) (0.095) (0.101) (0.142)

Sample Size 6.6e-4 4.9e-4 1.7e-5 -3.1e-4

(4.8e-4) (7.2e-4) (5.4e-4) (7.2e-4)

Constant 0.380*** 0.383*** 0.355*** 0.178

(0.117) (0.120) (0.114) (0.153)

R2 (adjusted in Metaregs) 0.175 0.196 0.117 0.174

N 262 179 204 160

Notes: *** p<0.01, ** p<0.05, * p<0.1; LPMa1 is linear probability model run on the sample for which discrimination can only be taste-based, LPMa2 is linear probability model run on the sample for which dicrimination can be both taste-based and statistical, Metareg1 is meta-regression run on the sample for which discrimination can only be taste-based and effect sizes are available, Metareg2 is meta-regression run on the sample for which discrimination can be both taste-based and statistical and effect sizes are available; 'test of coefficient difference' reports whether coefficients differ significantly between models 1 and 2; the omitted category is Artificial (identity); errors in LPM models are corrected for heteroskedasticity, with 65 clusters in LPMa1 and 59 in LPMa2; standard errors in parentheses.

68

Table C.6b: Linear Restriction Tests on models presented in Table C.6a

Null Hypothesis

P Value on two-tailed test

LPMa1 LPMa2 Metareg1 Metareg2

Ethnicity = Religion 0.171 0.876 0.38 0.756

Ethnicity = Nationality 0.353 0.788 0.87 0.405

Ethnicity = Gender 0.348 0.045** 0.163 0.003***

Ethnicity = Soc/Geo Groupings 0.002*** <0.001*** 0.016** 0.005***

Ethnicity = Natural Other 0.052* 0.911 0.977 0.373

Religion = Nationality 0.082* 0.989 0.509 0.699

Religion = Gender 0.097* 0.413 0.878 0.020**

Religion = Soc/Geo Groupings <0.001*** 0.013** <0.005*** 0.006***

Religion = Natural Other 0.018** 0.839 0.679 0.532

Nationality = Gender 0.985 0.057* 0.29 0.005***

Nationality = Soc/Geo Groupings 0.012** <0.001*** 0.04** <0.001***

Nationality = Natural Other 0.099* 0.823 0.974 0.745

Gender = Soc/Geo Groupings 0.015** <0.001*** 0.003*** <0.001***

Gender = Natural Other 0.097* 0.624 0.613 0.192

Soc/Geo Groupings = Natural Other 0.81 0.015** 0.33 0.007

Note: *** p<0.01, ** p<0.05, * p<0.1

69

Chapter Three: On the social

inappropriateness of

discrimination31

Abstract

We experimentally investigate the relationship between discriminatory behaviour and

the perceived social inappropriateness of discrimination. We test the framework of

Akerlof and Kranton (2000, 2005), which suggests discrimination will be stronger

when social norms favour it. Our results support this prediction. Using a Krupka-

Weber social norm elicitation task, we find participants perceive it to be less socially

inappropriate to discriminate on the basis of social identities artificially induced,

using a trivial minimal group technique, than on the basis of nationality.

Correspondingly, we find that participants discriminate more in the artificial identity

setting. Our results suggest norms and the preference to comply with them affect

discriminatory decisions and that the social inappropriateness of discrimination

moderates discriminatory behaviour.

JEL classifications: C71 – Cooperative games; C92 – Laboratory Experiments (Group

Behavior); D03 – Behavioral Microeconomics: Underlying Principles

Keywords: Discrimination; Social norms; Krupka-Weber method; Allocator game

31 This chapter was co-authored with Abigail Barr and Daniele Nosenzo.

70

1. Introduction

Economic theories seeking to explain discrimination focus on two mechanisms. First,

in the presence of incomplete information, profit- or income-maximizing agents use

aggregate group characteristics to form statistical beliefs about individual

characteristics and then act in accordance with those beliefs by, potentially, treating

members of different groups differentially (Arrow, 1972). Second, individuals are

assumed to derive direct utility from favouring certain groups relative to others, i.e.

they are assumed to have a ‘taste for discrimination’ (Becker, 1957). Such tastes

explain why discrimination is observed even in settings where asymmetric or

incomplete information is not an issue (e.g. Chen and Li, 2009; Abbink and Harris,

2012). However, given their empirical importance, the psychological foundations of

such tastes or preferences for discrimination have received remarkably little attention

in the literature.

In this paper we use experimental methods to test whether tastes for discrimination

are systematically shaped by social norms, i.e. by collectively recognised rules of

behaviour that define which actions are viewed as socially appropriate within a

specific social group.32 The importance of norms for discriminatory behaviour has

been suggested by Akerlof and Kranton (2000, 2005). In their framework, individuals

mentally place themselves in social categories (or identity groups), thereby assigning

themselves social identities.33 They have perceptions of the specific prescriptions

(norms) that mandate how individuals within these identity groups are expected to

behave, and gain utility from conforming to the prescriptions that apply to their own

group, as it ‘affirms [their] self-image, or identity’ (Akerlof and Kranton, 2000, p.

716). Within this framework, intergroup discrimination arises if the behaviours that

are prescribed to the members of one group involve differential treatment or

consideration of in-group and out-group members.34

32 See Elster (1989) and Ostrom (2000) for definitions of social norms.

33 See also Huang and Wu (1994) and Montgomery (1994) for related approaches.

34 As an extreme example, consider the case of caste discrimination in South Asia and the belief that

caste 'purity' (identity) can be 'polluted' by interactions with the individuals at the bottom of the

caste system (known as 'Dalits'). This led to the so-called 'untouchability practices', a set of

strongly discriminatory norms against Dalits, which, for example, impose segregation and

71

The Akerlof and Kranton framework implies a positive correlation between in-group

members’ beliefs about the appropriateness of discrimination and the incidence of

discriminatory behaviour. Similar correlations have been found in relation to other

types of economic behaviour. Following Krupka and Weber (2013), experiments have

shown that in a variety of economic contexts people are more likely to take an action

if they perceive it to be more socially appropriate (e.g. Burks and Krupka, 2012 –

corporate ethics; Gachter et al, 2013 – gift-exchange; Krupka et al, 2016 – informal

contract enforcement; Banerjee, 2016 – bribery). There is also non-experimental

evidence suggesting norms drive economically-relevant behaviour (e.g. Buonanno et

al, 2009). Therefore, economists are increasingly invoking social norms and norm-

compliance to explain empirical behaviour. In driving behaviour, social norms may

effectively substitute for laws (e.g. Huang and Wu, 1994), or may complement them

(e.g. Sunstein, 1990; Kubler, 2001; Lazzarini et al, 2004; Posner, 2009; Benabou and

Tirole, 2011).

However, a correlation between individuals’ beliefs about the appropriateness of

discrimination and the prevalence of discriminatory behaviour is a challenge to

empirically document using naturally occurring data, not least of all because of the

difficulties associated with accurately measuring such beliefs.35

Occasionally, attitudinal surveys include questions that can be interpreted as eliciting

respondents’ perceptions of the appropriateness of discrimination. For instance, the

2002 wave of the Scottish Social Attitudes Survey asked respondents whether they

believed that ‘sometimes there is good reason for people to be prejudiced against

certain groups’. One can interpret positive responses to this question as an imperfect

proxy for the perceived social appropriateness of racial discrimination. Using this

interpretation, we calculated the percentage of residents in each local authority area of

Scotland who agreed with the survey question. For each area, Figure 1 plots this

restrictions on occupation, prohibit inter-caste marriage, and limit or prohibit access to public

places and services.

35 See Krupka and Weber (2013) and Mackie et al. (2015) for a discussion of the difficulties of

measuring social norms empirically.

72

variable against the number of racist incidents36, per 100 non-white residents37,

reported to the police in the financial year 2003-4 (Scottish Executive Statistical

Bulletin, 2007). A correlation of 0.27 between the two variables indicates a positive

relationship between the social appropriateness of racial discrimination and the

incidence of racially discriminatory behaviour, which is consistent with the Akerlof

and Kranton framework.

The acceptability of prejudiced-based humour has sometimes been used as a proxy

for the normative appropriateness of discrimination (see, e.g., Crandall et al., 2002).

Figure 2 plots, over the period 2004 to 2014, the frequency of Google searches in the

US for ‘N***** jokes’ (we apply the censorship for this paper; the original search

term was uncensored38), as a proportion of all Google searches in the US (Google

Trends, 2016). Searching for racist jokes about black people can be treated as

evidence that the searcher perceives discrimination against black people to be socially

appropriate. Figure 2 also plots, on an annual basis over the same period, the number

of incidents in the US involving hate crimes motivated by an anti-black bias that were

reported to the FBI, per every 100 people living in areas where the hate crimes are

reported39 (United States Department of Justice, 2005, 2006, 2007, 2008, 2009, 2010,

2011, 2012, 2013, 2014, 2015). Both the frequency of anti-black joke searches and

the rate of anti-black hate crime incidents declined considerably over the period. This

is suggestive of a positive relationship in the US between the change over time in the

social appropriateness of discrimination against black people and the change over

time in discriminatory behaviour against black people.

36 The Scottish police define a racist incident as ‘any incident which is perceived to be racist by the

victim or any other person.’ (Scottish Executive Statistical Bulletin, 2007)

37 The contemporaneous proportion of non-white residents in each Scottish local area is taken from

the 2001 UK Census (National Records of Scotland, 2011).

38 We deliberated over our decision to censor the word, but eventually concluded that we felt

uncomfortable using it uncensored even in a scientific context. We expect readers will be able to

guess the extremely derogatory term describing black people that we refer to.

39 We report this, rather than the absolute number of hate crimes, to adjust for the fact that the

population covered by the FBI’s hate crime statistics varies from year to year. The proportion of

black people in the covered population is not available.

73

Figure 1: Variations in attitudes towards racial prejudice and race crimes across

Scottish local authority areas

Note: Figure 1 plots, at the level of local authority area, the relationship between

attitudes to prejudice, as reported in the Scottish Social Attitudes Survey 2002, and

the frequency of racist incidents reported to the police in the financial year 2003-4.

Each data-point represents one local authority area in Scotland.

74

Figure 2: Google searches for racist jokes about black people and anti-black hate

crimes in the US, 2004-14

Note: The light grey line plots the number of anti-black hate crime incidents reported

to the FBI each year, adjusted for the population size covered by reporting agencies

at the time. The dark grey line plots the relative frequency, amongst Google searches

in the US, of the search term ‘N***** jokes’ (censorship applied retrospectively) –

monthly data was recovered using the Google Trends tool, and is averaged over the

course of each year.

In spite of these examples, the paucity of useful naturally occurring data with which

to investigate the empirical relevance of Akerlof and Kranton’s framework to the

issue of discrimination advances the case for using experimental methods to address

the question. Our paper does this, with an empirical strategy relying on four main

elements.

First, we use standard experimental techniques to prime participants to think about

particular dimensions of their identities. The priming aims to trigger the process of

social identification that is central to Akerlof and Kranton’s approach by encouraging

75

subjects to identify with half of the participants in their experimental session and not

with the other half.

Second, in the decision-making phase of the experiment we ask subjects to distribute

a given amount of money between two potential recipients, one an individual sharing

their primed identity, the other an individual not sharing their primed identity. This

simple allocation task allows us to measure discrimination as the extent to which

individuals are willing to favour members of their own social group at the expense of

the out-group.

Third, we vary the dimension of identity that is primed. Applying Akerlof and

Kranton’s framework, the distributive decision that an individual makes within our

experiment will depend on the normative prescriptions that apply, given the

individual’s own social identity and the way the social identities of each of the two

recipients relate to it. This implies that the content of the normative prescriptions

pertaining to discrimination depend on what dimension of identity is salient within

the decision-making context.40 Focusing on this aspect of Akerlof and Kranton's

framework, we design two identity treatments, aimed at inducing different

perceptions of the appropriateness of discrimination, while holding other aspects of

the decision-making context constant. Under one treatment, social identities are based

on nationality; we form groups in the laboratory based on whether participants are

British or Chinese. Under the other treatment, social identities are entirely artificial;

groups are formed according to the colour of ball that each participant draws blindly

from a bag. We expect the prescriptions that mandate how a decision-maker should

treat in-groups and out-groups in our experiment to differ across the two treatments.

Specifically, we expect discrimination against out-group and in favour of in-group

members to be perceived as less appropriate when identity groups are formed on the

basis of nationality, than when they are artificially formed on the basis of the colour

40 For example, norms may render it appropriate to discriminate against others who support a

different football team or listen to a different type of music from oneself, but not appropriate to

discriminate against others who are different in terms of ethnicity or gender; and individuals may

moderate their behaviour accordingly.

76

of balls randomly picked. Therefore, if discrimination is systematically shaped by

norms, we expect discrimination to be stronger between the artificial groups.

Fourth, as well as measuring discrimination, we directly measure the perceived social

appropriateness of discrimination in each treatment. We do this by employing the

'norm-elicitation' task introduced by Krupka and Weber (2013), in which participants

are described the allocation game and are asked to evaluate the social appropriateness

of each and every possible action available to the allocator. We use this norm-

elicitation task to construct an incentivized measure of the extent to which

participants’ perceptions of the appropriateness of discrimination vary across our two

treatments and to examine the extent to which these differences in perceived

appropriateness translate into differences in discriminatory behaviour in the allocation

task.

Our results show that, in both treatments, discriminatory actions are viewed as

socially inappropriate. However, as expected, discrimination is perceived to be

significantly less appropriate in the nationality treatment compared to the artificial

identity treatment. The results of the decision task match these differences in

perceived appropriateness: while few participants discriminate in either treatment,

discrimination is significantly stronger between artificial groups than between

nationality groups. These results are consistent with the Akerlof-Kranton framework:

the perceived social appropriateness of discrimination varies according to the way

identity groups are defined, and this forms the basis for individuals’ revealed

preferences for discrimination.

Our study’s main contribution is in linking discrimination to social norms and social

identity theory. In this sense, our study is closely related to the paper by Chang et al.

(2015), who apply Akerlof and Kranton's framework to investigate the effect of

priming US citizens’ political identities on redistributive behaviour. They show that

individuals' primed political identities (Democratic or Republican) determine their

perceptions of the social appropriateness of redistribution, and that this explains

differences in redistributive behaviour between Democrats and Republicans. Like

Chang et al., our experiment also shows that both individuals’ distributive decisions

and their perceptions of the social appropriateness of such decisions are sensitive to

77

the dimension of identity that is salient in a given context. However, while the

normative prescriptions upon which Chang et al focus relate to the social identity of

the decision-maker alone, we focus on the social identities of both the decision-

makers and other individuals affected by their behaviour, and on how those social

identities relate one to another. Thus, unlike Chang et al., in our experiment both the

priming and the distributive decisions have an intergroup component which allows us

to investigate the relationship between social identities, social norms, and

discriminatory behaviour.

Our paper is also related to work on the associations between social identity and norm

enforcement.41 Bernhard et al. (2006) and Goette et al. (2006), for instance, use third-

party punishment games to study whether the willingness to enforce norms of sharing

and cooperation depends on the social identities of the norm violator and of the victim

of the norm violation and on how those identities relate to that of the norm enforcer.

Both papers find that social identity systematically affects the patterns of norm

enforcement: enforcers are generally more willing to mete out punishment against

violators when the victim of the norm violation is an in-group rather than an out-

group member. Also related is Harris et al. (2014), who study whether in-group

favouritism is proscribed by social norms by observing the extent to which

individuals are willing to incur costs to punish it. They find that in-group favouritism

goes largely unpunished when the punisher belongs to the same identity group as the

norm violator or when she belongs to a neutral group. In-group favouritism is instead

frequently punished when the punisher belongs to a different identity group. Harris et

al. conclude that in-group favouritism is not always considered a violation of social

norms, as this depends on the identities of the agents involved in the interaction.

41 Also relevant is the research, mostly undertaken by psychologists, on the associations between

social norms and the expressions of prejudiced views – a related but different phenomenon to

acts of discrimination. Crandall et al (2002), for instance, found that expressions of prejudice

towards groups are very strongly correlated with reported beliefs on the social appropriateness of

such prejudice. Other studies have shown that the degree to which individuals are willing to

express prejudice can easily be swayed by the views of others (Blanchard et al, 1994; Zitek and

Hebl, 2007), or by an experimenter deceptively varying the social norm that is presented to them

(Nesdale et al, 2005), suggesting that normative consideration may play an important role on the

expression of prejudice.

78

While these studies strongly suggest an association between discrimination and social

norms and identities, none of them has directly measured the norms that underlie the

observed patterns of behaviour. Moreover, none of these studies has investigated

whether variations in primed social identity trigger differences in norms that, in turn,

predict variations in discrimination. Thus, our study fills an important gap in this

literature, as we are the first to provide direct evidence not only that discrimination

co-varies with group norms, but also that these norms vary across particular

dimensions of an individual’s identity.

The rest of the paper is set out as follows: Section 2 sketches a simple theoretical

model of identity and norm-compliance that we use to motivate and inform our

empirical strategy. Section 3 outlines our experimental design; Section 4 presents our

results; Section 5 concludes and discusses our findings.

2. Theoretical framework

Our simple model of social norm-compliance closely follows Krupka and Weber

(2013), and in particular Chang et al (2015), who based theirs on Akerlof and Kranton

(2000, 2005). We first assume that individuals have multiple social identities, the

salience of which depends on the decision-making context.

An individual 𝑖’s utility 𝑈𝑖 depends on the actions of him- or herself and others,

𝑎 = (𝑎𝑖, 𝑎−𝑖), and the salient social identities of him- or herself and others,

𝐼 = (𝐼𝑖, 𝐼−𝑖):

𝑈𝑖(𝑎, 𝐼) = 𝑉𝑖(𝑎) + 𝛾𝑖𝑁(𝑎𝑖|𝑎−𝑖, 𝐼)

We assume that the decision-maker’s utility can be broken into two components. The

first component, 𝑉𝑖(𝑎), describes individual 𝑖's utility over material payoffs, which in

turn depend upon his or her own actions and the actions of others. Note that this

accommodates standard self-regarding preferences, where the individual only cares

about his or her own material payoff, as well as various forms of outcome-based

other-regarding preferences, where individual 𝑖's utility also depends on others’

material payoffs (e.g. Fehr and Schmidt, 1999; Bolton and Ockenfels, 2000).

79

The second component of utility is derived from complying with normative

prescriptions and is captured by the function 𝑁(. ). The normative prescriptions

define, for each action 𝑎𝑖 available to individual 𝑖, the social appropriateness of that

action, given the actions of other players. Crucially, as in Akerlof and Kranton (2000,

2005), we assume that normative prescriptions also depend on the salient identities of

𝑖 and other players, and on how these relate to one another. This takes into account

that differently defined identity groups may normatively prescribe different

behaviours, and therefore that the same action may be viewed as more or less socially

appropriate depending on the salient dimension of the identity of the decision-maker

in a given context, as well as the identities of the other players with whom the

decision-maker interacts. Finally, 𝛾𝑖 is an individual-specific parameter defining the

importance that individual 𝑖 attaches to complying with social norms.

In our experiment, subjects face a simple allocation task (described in detail in the

next section), which measures the extent to which they are willing to treat differently

those who belong to the same identity group as themselves from those who belong to

a different one. In all treatments of the experiment, we keep constant the set of

material payoffs available to players and the mapping from actions into payoffs. Thus,

the first component 𝑉𝑖(𝑎) of the utility function above is held constant across

treatments.

Our treatments vary the dimension of identity 𝐼 that is made salient to the decision-

makers and, hence, the process by which the relevant identity groups are defined in

the experiment. As we describe in detail in the next section, in one treatment

participants are encouraged to form identity groups on the basis of a random event,

while in the other treatment identity groups are based on a meaningful personal

characteristic. An implication of this treatment manipulation is that the normative

prescriptions, 𝑁(𝑎𝑖|𝑎−𝑖, 𝐼), that regulate the second component of the utility function

described above may differ across treatments. Specifically, the same action 𝑎𝑖

available to the decision-maker may be evaluated differently depending on how

identity groups are formed. We employ a norm-elicitation technique, based on the

task introduced by Krupka and Weber (2013), to quantify, in an incentive-compatible

way, the function 𝑁(. ) in each treatment. This allows us to assess the extent to which

normative prescriptions do indeed differ across treatments; and therefore to examine

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the extent to which differences between treatments in the level of discrimination in

the allocation task are explained by differences in the perception of its

appropriateness.

3. Experimental design

Measuring discrimination – the allocator game

In the allocator game, one participant was endowed with £16 and asked to allocate it

between two passive players, one belonging to his or her own identity group and the

other belonging to a different identity group.42 The decision-maker could not keep

any of the money for him- or herself but knew he or she would receive a payment,

between £6 and £10, which the computer would randomly pick at the end of the

experiment.43 Allocators could split the money any way they liked between the other

two players, as long as each amount was a multiple of two. Thus, the allocator had to

choose one of nine possible allocations of money between the two passive players,

ranging from (£16; £0) to (£0; £16). In order to maximize sample sizes, we elicited

decisions using a role randomisation method: all participants were asked to make a

decision in the allocator role knowing that their actual role would be determined at

random at the end of the experiment (participants had a one-third chance of being

assigned the allocator role and a two-thirds chance of being assigned the passive

player role). Role assignment was implemented at the end of experiment, once

everyone had submitted an allocation decision. Decisions were made anonymously

and the only information allocators had about their recipients was the identity group

that each of them belonged to.

We chose the allocator game as our discrimination-eliciting device for the following

reasons. First, given our focus on the micro-foundations of taste-based discrimination,

we wanted a decision-making task within which statistical discrimination had no

relevance; in the allocator game the decision-maker’s material payoff does not

42 See Supplementary Online Materials A for a copy of the instructions used in the experiments.

43 The possible payments were £6, £8 and £10; each had 1/3 probability of occurring. Our aim was to

pay allocators £8 on average. However, had we had made this payoff a certainty it might have

inflated the salience of the (8,8) split in the allocator game, as this allocation would ensure payoff

equality across all three players.

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depend on what any other player does, so statistical beliefs about other players are

irrelevant.44 Second, to maximise our chances of discerning treatment differences, we

wanted a task that reliably produces discriminatory behaviour; in a meta-analysis

Lane (forthcoming) found the allocator game to be the experimental task that yielded

the strongest discrimination. Finally, in the allocator game, discrimination is

measured within-participants, so it is obvious to participants what the experiment is

about and any observed discrimination is interpretable as conscious rather than

subconscious. Thus, the game is an ideal subject for a norm-elicitation task; it is much

simpler to assess the social appropriateness of conscious behaviour than of

subconscious behaviour.

Measuring the social appropriateness of discrimination – the Krupka-Weber

norm-elicitation task

We elicited the social appropriateness of discrimination in the allocator game using

an adaptation of the task design pioneered by Krupka and Weber (2013). Participants

were described the allocator game, were presented with a table listing the nine

possible actions the allocator could take, and were asked to evaluate the social

appropriateness of each by marking one option on a four-point scale: ‘Very socially

inappropriate’, ‘Somewhat socially inappropriate’, ‘Somewhat socially appropriate’

or ‘Very socially appropriate.’ To ensure that the relevant perceptions of

appropriateness are measured, the evaluators should be, to the greatest extent

possible, in the mind-set of the person making the decision they are evaluating. In our

experiment, participants in the norm-elicitation task were the same as those playing

the allocator game, although we varied which task came first (participants were

unaware of the content of the second task until they had completed the first). All

participants were assigned to identity groups before their first task, so those taking the

norm-elicitation task first had had their identities primed in exactly the same way as

the allocator game participants whose behaviour they were evaluating. Each

44 Note that given the non-strategic nature of the allocator game certain elements of the utility

function set out in the previous section are redundant. This notwithstanding the proposed

framework remains relevant. In section 4, for the purpose of analysis, we set out a parameterised

version of the utility function that is directly and entirely relevant to the game.

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individual in the norm-elicitation task only evaluated the appropriateness of actions

made by allocators of the same identity group as that individual.

The evaluation of actions was incentivised. Participants were told that, at the end of

the experiment, one of the nine actions they had evaluated would be randomly

selected, and each participant’s evaluation of the action would be compared to that of

another randomly selected participant. If a participant’s evaluation matched that of

the person they were compared with, that participant would earn £8; otherwise they

would earn nothing. The incentives transform the task into a coordination game,

where participants are incentivised to match other participants’ evaluations of

appropriateness. Krupka and Weber (2013) argue that this gives participants an

incentive to reveal their perception of what is commonly regarded as appropriate or

inappropriate behaviour in the decision situation, rather than their own personal

evaluation of the actions they are asked to consider. This is important because social

norms are collectively recognized rules of behaviour, rather than personal opinions

about appropriate behaviours (e.g. Elster, 1989; Ostrom 2000).

Moreover, because we wanted to incentivise participants to coordinate on identity-

specific social norms (i.e. the social norms that were recognised by those belonging to

a specific identity group), participants were told that the person whose evaluation

theirs would be compared to would be a member of their own identity group.

Participants were told:

‘By socially appropriate, we mean behaviour that you think most

participants [of your group] would agree is the "correct" thing to do.

Another way to think about what we mean is that if [the allocator]

were to select a socially inappropriate action, then another participant

[of your group] might be angry at [the allocator].’

Treatments

Our treatments, labelled Nationality and Artificial, differed in the way identity groups

were formed. In Nationality participants in the experiment were segregated into

identity groups based on nationality (previous economics studies taking this approach

include Hennig-Schmidt et al, 2007; Netzer and Sutter, 2009; Guillen and Ji, 2011).

In Artificial participants were split into ‘minimal groups’, using a variant of the

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technique first introduced by Tajfel et al (1971), wherein social identities are

artificially instilled in participants during the experiment.

For both treatments we recruited British and Chinese students at the UK campus of

the University of Nottingham, a British institution which hosts a large number of

students from China.45 In the Nationality treatment, upon arrival, the British were

seated on one side of the lab and the Chinese on the other. At every computer

terminal on the British (Chinese) side was placed a sign reading ‘YOU ARE ON THE

BRITISH (CHINESE) SIDE OF THE ROOM. ALL PARTICIPANTS ON THIS

SIDE OF THE ROOM ARE BRITISH (CHINESE)’ (see Supplementary Online

Materials B). In the instructions at the beginning of the experiment, it was again made

explicitly clear that the lab and the participants had been divided based on nationality.

In the Artificial treatment, upon arrival, participants blindly drew a ball from a bag. In

each session the bag initially contained equal numbers of green and yellow balls, and

participants continued to draw from it until the bag was empty, thus ensuring an equal

split of green and yellow balls drawn. Those with green balls were then seated on one

side of the lab, and those with yellow on the other. Consistent with the Nationality

treatment, signs were placed at each terminal, reading ‘YOU ARE ON THE

(GREEN/YELLOW) SIDE OF THE ROOM. ALL PARTICIPANTS ON THIS SIDE

OF THE ROOM DREW A (GREEN/YELLOW) BALL’, and it was again made

explicit at the beginning of the instructions that the lab and the participants had been

divided on the basis of ball colour.

45 Participants were recruited using ORSEE (Greiner, 2015), an online database of experimental

participants, upon which participants are asked to state their nationality when they sign up. We

were able to cross-check nationalities using the University of Nottingham’s central student register

system, which lists students’ official nationalities. Note that we based the groups in our

experiment on official nationalities, rather than self-identified ones (e.g. we did not invite

Malaysian students who listed their nationality as Chinese). Chinese participants were

mainlanders, with none from Hong Kong, Macao or Taiwan.

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As in the Nationality treatment, we invited an equal mix of British and Chinese

students to the Artificial sessions. This ensures comparability between the two

treatments.46

We chose our treatment manipulation because we conjectured that it would produce

the differences that we needed to test the Akerlof and Kranton framework.

Specifically, we conjectured that discrimination would be stronger in the Artificial

compared to the Nationality condition. This conjecture was based primarily on

existing evidence from previous research: experiments priming national identity (e.g.

Hennig-Schmidt et al, 2007; Netzer and Sutter, 2009; Willinger et al, 2003) have

often not found significant discrimination, while experiments involving minimal

group identity (e.g., Ahmed, 2007; Chen and Li, 2009; Hargreaves-Heap and Zizzo,

2009) do so more frequently, and according to a recent meta-analysis by Lane

(forthcoming), on average, discrimination is significantly weaker in the former

compared to the latter type of experiment. There are also theoretical reasons why

discrimination would be stronger in the Artificial condition. First, members of newly

formed groups may be more inclined to draw boundaries between in- and out-groups

than members of more established groups (Jetten et al., 1996). In our experiment, the

groups in the Artificial treatment are new, while those in the Nationality treatment are

not. Second and more closely related to the theoretical framework above, the extent to

which individuals are willing to behave prejudicially may be related to how easily the

expression of prejudice can be justified to oneself or others (Crandall et al., 2002).47

In our experiment, discrimination against people who randomly drew a ball of a

46 Given the relatively small Chinese community in Nottingham, Chinese participants in our

experiment were more likely to know each other than were the British. This could be problematic

if, particularly in the Nationality treatment, participants based their behaviour on the number of

friends they had on either side of the lab. We controlled for this by asking each participant, in the

post-experimental questionnaire, how many people on each side of the lab they had previously

met. Chinese participants were indeed more likely to know each other, but there was no

association between the number of friends on either side of the lab and participants’ behaviour in

either treatment (available on request).

47 For instance, Crandall et al. (2002) show that there are large differences in the perceived

appropriateness of prejudice against Blacks vis-à-vis members of the American Nazi Party. They

argue that this is related to the differences in “… an outside perceiver’s sense of the justification of

the prejudices …. the justifications of the prejudice against Nazis are widely accepted; the

justifications of the prejudice against Blacks are not.” (p. 361).

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different colour may be easier to justify than discrimination on the basis of

nationality. Third and again closely related to the theoretical framework, relatively

weak norms against discrimination in the Artificial treatment could arise because it

triggers group identity akin to sports fandom, a dimension of identity across which

discrimination, via competition, is expected. In contrast, there may be stronger norms

proscribing discrimination against foreign nationals, given the historical sensitivities

this could arouse.

Procedure

All participants participated in both the allocator game and the norm-elicitation task,

as well as completing a post-experimental questionnaire. In each session, everyone

received payment either for the allocator game or for the norm-elicitation task, as

determined by a coin toss at the end of the experiment. Participants also received a £4

show-up fee. The order in which the tasks were performed was randomised between

sessions, so that we could check for ordering effects. We do not find such effects (see

Supplementary Online Materials C for the analysis), which is consistent with the

findings of Erkut et al (2015) and D’Adda et al (2016). Therefore, in the analysis

below we pool across ordering conditions. All sessions had 24 participants – twelve

belonging to each group – and were conducted in March or April 2015, using z-Tree

(Fischbacher, 2007). We conducted ten sessions, with 120 participants participating

in each treatment.48

4. Results

Treatment differences – social norms

We look first at the social appropriateness of discrimination in each treatment, as

measured by the norm-elicitation task. Figure 3 plots the mean appropriateness

ratings assigned to each allocation in the Nationality and Artificial treatments.

Following the approach of Krupka and Weber (2013), we assign evenly-spaced

values of -1 for the rating ‘very socially inappropriate’, -0.33 for the rating

48 We conducted one additional session in the Artificial treatment which we exclude from the analysis.

This is due to procedural issues that resulted from a low turn-up rate. Excluding the session does

not meaningfully affect any important results.

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‘somewhat socially inappropriate’, 0.33 for the rating ‘somewhat socially

appropriate’ and 1 for the rating ‘very socially appropriate.’ The table at the bottom

of the figure displays the distribution of evaluations for each allocation in each

treatment, and presents the results of randomisation tests on the treatment differences

in mean ratings. Our results are corrected for the fact that we are performing multiple

tests; applying the Benjamini-Hochberg False Discovery Rate method (Benjamini and

Hochberg, 1995), we sort our p-values in ascending rank and multiply each by the

number of separate tests being performed (in our case nine, one for each possible

allocation) before dividing each by its rank – thus the greatest adjustment is made to

smaller p-values.49

In each treatment the mean and modal evaluations follow the same general pattern.

Participants tend to regard extreme discrimination against recipients belonging to

either identity group to be very socially inappropriate, while the equal split is

generally regarded as very socially appropriate. There is a lack of strong consensus on

allocations mildly favouring members of one group or the other. This pattern is

consistent with a social norm of equality. However, in both treatments the perceived

social appropriateness decays faster as allocations move away from equality towards

favouring the out-group member than when they move towards favouring the in-

group member, indicating that social norms against discrimination are stronger when

the victim is a member of one’s own identity group.50

By design, any treatment differences in the ratings assigned to a given allocation can

only be driven by contextual differences in the perceived appropriateness of

discrimination. We observe subtle but significant treatment differences. Whereas 95%

of participants in the Nationality treatment perceive the equal split to be very

appropriate, the equivalent figure is only 84.2% in the Artificial treatment; mean

49 All p-values reported in this paper are two-sided and based on Fisher randomisation tests and

corrected using the Benjamini-Hochberg False Discovery Rate method. See Moir (1998) for a

discussion of the randomisation test, and Kaiser and Lacy (2009) for information on the Stata

command used to apply it.

50 OLS regressions confirm that, in both treatments, the rate of decay of appropriateness of

allocations favouring the out-group is significantly higher than that of allocations favouring the in-

group (both p-values < 0.002).

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ratings for the equal split are significantly higher in the Nationality treatment.

Furthermore, as the allocations move away from the equal split towards favouring the

in-group, the appropriateness ratings decline at a faster rate in the Nationality

treatment than in the Artificial treatment. For the extreme (16,0) split, 92.5% of

participants in the Nationality treatment opt for ‘very inappropriate’, while only

80.8% do so in the Artificial treatment. And while only 5% of participants rate the

(16,0) allocation as socially appropriate in the Nationality treatment, 18% do so in the

Artificial treatment. In fact, Figure 3 shows that, for any in-group-favouring

allocation, there are more participants in the Artificial than Nationality treatment who

find discrimination to be socially appropriate.51

As a consequence, all in-group-favouring allocations are on average perceived to be

more appropriate in the Artificial treatment, and the differences are statistically

significant at the 5% level or lower in three out of four possible

51 In Supplementary Online Materials D we show that these treatment differences in the perceived

norms are driven by variations in the within-subject response patterns to the norm-elicitation task

across treatments. In particular, in the Artificial treatment we find relatively more subjects who

assign their highest appropriateness rating to the (16,0) allocation and then monotonically

decrease their ratings of appropriateness as more money is given to the out-group member. Such

a pattern indicates the perception of a social norm of in-group favouritism.

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Figure 3: Perceived social appropriateness of actions in allocator game

Notes: Figure 3 presents the distribution of social appropriateness ratings of each allocation in the two

treatments. Allocations (e.g. 16,0) are denoted by the amount given to the in-group member on the left (£16),

and the amount given to the out-group member on the right (£0). Shaded cells represent the modal ratings for

each allocation in each treatment. Mean ratings are taken by assigning values of 1, 0.33, -0.33 and -1 for the

ratings ‘very appropriate’, ‘somewhat appropriate’, ‘somewhat inappropriate’ and ‘very inappropriate’

respectively, and averaging the values for all participants in a given treatment. Benjamini-Hochberg-corrected

p-values are reported from randomisation tests.

89

cases (the exception being the allocation 14,2 for which the difference is significant at

the 10% level). Moreover, the differences in perception of appropriateness of

discrimination only pertain to in-group favouritism and not to any form of

discrimination; Figure 3 shows that, while out-group-favouring allocations are on

average perceived to be slightly more appropriate in the Artificial treatment, only for

the (6,10) allocation is the difference significant, and then only at the 10% level.52

Treatment differences – discrimination

Figure 4 shows the distribution of decisions made in the allocator game in each

treatment. In the Nationality treatment, 83.3% of participants choose to allocate the

money evenly between the in-group member and the out-group member. Only 69.2%

of the participants in the Artificial treatment make this choice. The remainder of

participants in each treatment discriminate against out-group members; no individual

in either treatment allocates more money to the out-group member than the in-group

member. 12.5% of participants in the Artificial treatment allocate all the money to the

in-group member, while only 4.2% do so in the Nationality treatment.

In the Nationality treatment, participants allocate an average of £8.67 to the in-group

member and £7.33 to the out-group member, resulting in a mean difference of £1.33.

In the Artificial treatment, participants allocate an average of £9.52 to the in-group

member and £6.48 to the out-group member, resulting in a mean difference of £3.03.

A randomisation test indicates that the mean difference in the Artificial treatment is

significantly higher than that in the Nationality treatment (p=0.007). This is consistent

with the conjecture that discrimination is stronger in the treatment where it is

perceived to be more socially appropriate. It suggests that norm-compliance

moderates discriminatory behaviour.

52 In Supplementary Online Materials E, we analyse cross-national differences in responses to the

norm-elicitation task. We show that in both the Artificial and Nationality treatments, Chinese

participants perceived discrimination to be more socially appropriate than British participants.

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Figure 4: Discrimination in the allocator game

Notes: Figure 4 shows the percentage of participants in each treatment

who choose each allocation. Allocations are denoted by the amount

given to the in-group member on the left, and the amount given to the

out-group member on the right – e.g. (16,0) denotes allocating £16 to

the in-group member and £0 to the out-group member.

In Table 1, an OLS regression confirms that the treatment effect on discrimination is

robust to the inclusion of various controls – such as age, gender, nationality and the

extent to which participants understand the tasks.53

53 In addition to the regression in Table 1, we ran further models on the British and Chinese

subsamples to investigate the effects on discrimination of several other variables which were

nationality-specific. These variables were not significant. For the British, we found no significant

effect on discrimination of: ethnicity, political persuasion, views on immigration, or hostility

towards foreign students. For the Chinese, we found no significant effect of: views towards

foreigners in China, feeling welcome in the UK, or hostility towards domestic students. Output is

available on request.

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Table 1: OLS regressions of treatment differences in discrimination

Dependent variable = Difference in amount allocated to

in-group member and out-group member

OLS model OLS model

Treatment

Artificial 1.700*** (0.605) 1.974*** (0.626)

Controls

Male 0.229 (0.664)

Age -0.121 (0.229)

Year of study -0.280 (0.379)

Chinese 2.212*** (0.802)

Misunderstanding 0.875 (0.687)

Rural background 0.637 (0.705)

Economics student -0.060 (0.775)

Constant 1.333 (0.428) 3.113 (4.003)

R2 0.032 0.082

N 240 234

Note: *** p<0.01, ** p<0.05, * p<0.1; Standard errors in parentheses.

Misunderstanding = number of control questions answered incorrectly at first

attempt; Six observations dropped from model with controls owing to missing data

for age and year of study.

Econometric analysis of individual behaviour

So far we have analysed the link between behaviour and norms at the group level, by

showing that there is more discrimination in the treatment where it is perceived as

less socially inappropriate. We now exploit the within-subject nature of our

experiment to extend the analysis to the individual level. Specifically, we investigate

whether a model that incorporates a preference for norm compliance is better able to

explain the behavioural regularities in our experiment than a model that does not

incorporate such a factor.

Following the theoretical framework introduced in section 2, we assume that the

utility that allocators derive from choosing allocation 𝑥 depends on two components,

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one defined on material payoffs and the other defined on normative prescriptions. We

assume that the first component depends on the absolute difference between the

material payoffs of the two passive players implied by allocation 𝑥. The second

component depends on the social appropriateness of the allocation. For allocator 𝑖,

𝑈𝑖(𝑎𝑥) = 𝑣|𝜋𝑗(𝑎𝑥) − 𝜋𝑘(𝑎𝑥)| + 𝛾𝑁𝑖(𝑎𝑥)

where 𝜋𝑗(𝑎𝑥) and 𝜋𝑘(𝑎𝑥) are the material payoffs that the two passive players 𝑗 and

𝑘 receive from allocation 𝑥, and 𝑁𝑖(𝑎𝑥) is the social appropriateness that allocator 𝑖

ascribes to allocation 𝑥, as measured in the norm-elicitation task.54

The parameter 𝑣 captures the weight that the allocator places on the material payoff

component of the utility function, while the parameter 𝛾 captures the weight that

allocators place on norms. Note that the material payoff component of the utility

function is blind to the identities of the passive players, and allocations that

implement unequal payoffs carry the same weight to utility, regardless of whether the

inequality favours the in-group or out-group. Thus, the parameter 𝑣 simply captures

(identity-blind) preferences associated with payoff inequality. In contrast, the

normative component of the utility function allows allocations to weigh differently in

the utility function depending on the identities of the passive players. Hence, the

parameter 𝛾 captures the weight that allocators place on a wider array of normative

considerations, including both norms of equality and identity-related prescriptions.55

Following Gaechter et al. (2013) and Krupka and Weber (2013), we use fixed-effects

conditional logit regressions to estimate the weights 𝑣 and 𝛾 on the two components

of the utility function. Specifically, we assume that allocators choose allocations

54 Recall that our experiment delivers, for each allocator 𝑖, a measurement of 𝑖's perceived social

appropriateness of allocation 𝑥. This is because each participant in our experiment made decisions

in both the allocation task and the norm-elicitation task.

55 While the allocation that equalises payoffs between passive players is a strict maximum for both the

first and second component of the utility function for many participants, this is not true for all. In

particular, about 15% of participants in Artificial and 3% in Nationality do not identify the equal-

split as the most socially appropriate allocation. Moreover, for another 7% of participants in

Artificial and 5% in Nationality the equal-split is not a strict maximum for the normative

component of the utility function.

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following a logit choice rule, whereby the likelihood of choosing each of the nine

possible allocations depends on the utility associated with that choice, 𝑈(𝑎𝑥), relative

to the utility associated with the alternative allocations:

𝑃𝑟(𝑎 = 𝑎𝑥) =𝑒𝑥𝑝{𝑈(𝑎𝑥)}

∑ 𝑒𝑥𝑝{𝑈(𝑎𝑙)}𝑙=1,…,9, 𝑥 = 1,… , 9

Our objective, here, is to show that a norm-augmented model is better able to capture

treatment differences in choices than a model which is identity-blind. Thus, in Table

2 we report the output of two fixed-effects conditional logit models, each estimated

using all of the allocation decisions and all of the social appropriateness evaluations

generated under either the Nationality or the Artificial treatment. In the first model we

impose the restriction 𝛾 = 0 to the utility function and, thus, estimate a choice model

where the decision-maker is purely concerned with identity-blind payoff inequality.

In the second model this restriction is removed and utility is allowed to depend on

both payoff inequality and wider normative prescriptions.

Table 2: Conditional logit regressions of the likelihood of choosing an

action

Dependent variable = 1 if action is chosen; 0 otherwise

Model (1) (2)

𝑣 (weight on payoff inequality) -0.338*** -0.111***

(0.021) (0.028)

𝛾 (weight on normative prescriptions) 1.081***

(0.119)

Pseudo R2 0.424 0.511

Bayesian Information Criterion 615.17 531.02

Number of Observations 2,160 2,160

Note: *** p<0.01, ** p<0.05, * p<0.1; Standard errors are in parentheses.

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The significant negative estimates of 𝑣 in both models indicate actions that yield

larger payoff inequality are less likely to be chosen. The significant positive estimate

of 𝛾 in model (2) indicates that more appropriate actions are more likely to be chosen.

The significant estimate of 𝛾 in a model that also includes the 𝑣 parameter indicates

that the normative component of the utility function can explain variation in choice

behaviour that cannot be entirely captured by pure (identity-blind) inequality

considerations. This also explains why the Bayesian Information Criterion is

significantly lower for model (2) than (1) (p < 0.001 on a likelihood-ratio test)

indicating that the norm-augmented model fits the data significantly better than the

model without norms.

The reason why the norm-augmented model performs better is made clear in Figure 5,

in which the aggregate action choice rates predicted by each of the models are

graphed next to the actual choice rates (as displayed in Figure 4). The left-hand panel

of Figure 5 presents the choice rates predicted by model (1). The right-hand panel

presents the choice rates predicted by model (2). For ease of comparison, actual

choice rates are reproduced in both panels. In each panel, the predicted choice rates

(striped bars) and actual choice rates (shaded bars) of the Nationality (Artificial)

treatment are shown in dark (light) grey.

The model in which participants are identity-blind and care only about inequality fails

to capture the most important features of the choice data. Most notably, the model is

unable to predict any treatment differences in choice, since the implied inequality of

an allocation is not different across the Artificial and Nationality treatments.

Moreover, the model predicts that deviations from equality are symmetric across the

choice space. That is, the probability of choosing an in-group-favouring allocation is

predicted to be the same as that of choosing an allocation which favours the out-group

by the equivalent amount. This is not the case in the actual choice data, as no-one

chooses out-group-favouring allocations, while 24% of participants choose an in-

group-favouring allocation.

In contrast, the norm-augmented model predicts a lower probability of choosing the

equal split allocation and higher probabilities of choosing in-group-favouring

allocations in the Artificial than Nationality treatment. This is in line with what we

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observed in the experiment. Moreover, although the model still assigns positive

probabilities to out-group-favouring allocations, it predicts lower probabilities for

them than for the comparable in-group-favouring allocations.

5. Conclusion

We show that discrimination is perceived to be socially inappropriate. However, the

extent of this perceived inappropriateness depends on the identities upon which

discrimination is based: when the identities are defined with reference to a brief,

random event, discrimination in favour of the in-

Figure 5: Actual choice rates in the allocator game and choice rates predicted by

conditional logits

Model with material payoff considerations only Norm-augmented model

Notes: Figure 5 shows the percentage of participants in each treatment who

choose each allocation, compared to the percentages of participants choosing

each allocation in each treatment as predicted by conditional logit models;

left-hand panel: model only taking into account considerations for material

payoffs, right-hand panel: model augmented by normative considerations;

allocations are denoted by the amount given to the in-group member followed

by amount given to the out-group member – e.g. (16,0) denotes allocating £16

to the in-group member and £0 to the out-group member.

96

group is viewed as more appropriate than when the identities are based on nationality.

Furthermore, we show that discrimination in the allocator game is stronger in the

setting where it is perceived to be more appropriate, and the econometric analysis

confirms that the differences in perceived appropriateness predict actual behaviour.

These findings are strongly supportive of Akerlof and Kranton (2000, 2005)

providing a useful framework within which to think about and model taste-based

discrimination. We offer direct evidence that differences in the way identity groups

are defined translate into differences in the perceived normative prescriptions, in

choice contexts that are otherwise identical. This offers direct support for Akerlof and

Kranton’s conjecture that the process of social identification plays a key role in the

formation of normative prescriptions.

Acknowledgements

This research was funded by the Economic and Social Research Council via the

Network for Integrated Behavioural Sciences (Award No. ES/K002201/1). We are

grateful for help provided in running the experiment by Erika Barbosa, Cindy Fu,

Xueheng Li and Till Weber. We received helpful comments at presentations at the

Universities of Nottingham and East Anglia from, amongst others, Despoina

Alempaki, Ben Beranek, Robin Cubitt and Emily Wyman, and we also received

helpful written advice from Ilyana Kuziemko.

97

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103

Supplementary Online Materials

A: Experimental instructions

A.1 Instructions for subjects in the Nationality treatment, playing allocator game first

Instructions

Welcome to this experiment. This is an experiment about decision-making. During the

experiment, we request that you remain quiet and do not attempt to communicate with other

participants. Participants not following this request may be asked to leave without receiving

payment. If you have any questions, please raise your hand and the experimenter will come to

you. For your participation, you will be paid a show-up fee of £4. You may also receive some

additional money based on your choices and the choices of others in the tasks described

below.

There will be two tasks for all participants to perform. At the end of the experiment, the

experimenter will toss a fair coin. If it lands on heads, all participants will receive payment

for the first task only; if it lands on tails, all participants will receive payment for the second

task only. As you will not know until the end of the experiment which task you will receive

payment for, please make your decisions in each task carefully. You will not receive feedback

on the outcome of any task until the end of the experiment, and your decisions in the first task

will have no effect on the nature or outcome of the second task. You will not receive any

instructions for or information about the second task until you have completed the first task.

After the second task, there will also be a questionnaire. The anonymity of your responses to

all parts of all tasks and questions is guaranteed.

Please now answer two questions on your screen, to ensure you understand the process of the

experiment.

In this experiment, the room has been divided into two sections on the basis of nationality. On

one side everyone is British; on the other side everyone is Chinese. The sign on your desk

reminds you whether you are on the British or Chinese side of the room.

104

Task One

In this experiment, one third of you will be randomly assigned by the computer into a role

entitled ‘Individual A’. The decisions made by Individual As during the task will determine

the payments from the task received by the other two thirds of participants. Each of you has

an equal chance of being an Individual A. Exactly who the Individual As are will not be

revealed until the end of the experiment. In the meantime, we ask all participants to make a

decision as if they are an Individual A.

Please make your decision carefully, as it may be used to determine participants’ payments.

Assume for the rest of this paragraph that you are an Individual A. Your task will be to decide

how to divide £16 between two other participants in the experiment, one who has the same

nationality as you, and another who has a different nationality from you. You may divide the

money any way you like so long as the amount allocated to each person is a multiple of two.

You may not allocate any of the money to yourself. However, you will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

Please now answer two questions on your screen, to ensure you understand this part of the

experiment.

105

Task Two

In the second part of this experiment, you will receive a description of a situation. This

description corresponds to a situation in which one person, “Individual A,” must decide how

to act. You will be given a description of various possible actions Individual A can choose to

take.

After you receive the description of the situation, you will be asked to evaluate each of the

various possible actions Individual A can choose to take. You must indicate, for each of the

possible actions, whether taking that action would be "socially appropriate" or "socially

inappropriate". By socially appropriate, we mean behaviour that you think most participants

of your nationality would agree is the "correct" thing to do. Another way to think about what

we mean is that if Individual A were to select a socially inappropriate action, then another

participant of your nationality might be angry at Individual A.

In each of your responses, we would like you to answer as truthfully as possible, based on

your opinions of what constitutes socially appropriate or socially inappropriate behaviour.

To give you an idea of how the experiment will proceed, we will go through an example

situation and show you how you will indicate your responses.

Example Situation

Individual A is at a local coffee shop near campus. While there, Individual A notices that

someone has left a wallet at one of the tables. Individual A must decide what to do. Individual

A can choose four possible actions: take the wallet, ask others nearby if the wallet belongs to

them, leave the wallet where it is, or give the wallet to the shop manager.

The table below presents the list of the possible actions Individual A can choose. For each of

the actions, you would be asked to indicate whether you believe choosing that action is very

socially inappropriate, somewhat socially inappropriate, somewhat socially appropriate, or

very socially appropriate. To indicate your response, you would click on the corresponding

button.

106

If this was the situation for this study, you would consider each of the possible actions above

and, for that action, indicate the extent to which you believe taking that action would be

"socially appropriate" or "socially inappropriate". Recall that by socially appropriate we mean

behaviour that most participants of your nationality agree is the "correct" thing to do.

For example, suppose you thought that taking the wallet was very socially inappropriate,

asking others nearby if the wallet belongs to them was somewhat socially appropriate,

leaving the wallet where it is was somewhat socially inappropriate, and giving the wallet to

the shop manager was very socially appropriate. Then you would indicate your responses as

follows:

If you have any questions about this example situation or about how to indicate your

responses, please raise your hand now.

You will next be given the description of a situation where Individual A, a participant in an

experiment, has to choose between various possible actions. After you read the description,

you must consider the possible actions and indicate on your computer screen how socially

appropriate these are in a table similar to the one shown above for the example situation.

After this, the computer will randomly select one participant of your nationality (that is, it

will select a British participant if you are British, or a Chinese participant if you are Chinese).

The computer will then randomly select one action Individual A can choose. Your evaluation

of this action will be compared with that of the randomly selected participant of your

nationality. If your evaluation is the same as theirs, you will receive £8 for this task;

otherwise you will receive zero.

For instance, imagine the example situation above was the actual situation and the possible

action "Leave the wallet where it is" was selected by the computer. If your evaluation had

been "somewhat socially inappropriate" then your task earnings would be £8 if the person

you are matched with also evaluated the action as “somewhat socially inappropriate” and zero

otherwise.

The situation

107

The situation you are asked to evaluate is like the one you participated in in the previous task.

Here is a summary.

Individual A is taking part in an experiment in this lab. The room has been divided into two

sections on the basis of nationality. On one side everyone is British; on the other side

everyone is Chinese. The anonymity of Individual A’s decisions in the experiment is

guaranteed.

Individual A’s task will be to decide how to divide £16 between two other participants in the

experiment, one who has the same nationality as Individual A, and another who has a

different nationality from Individual A. Individual A may divide the money any way he or she

likes so long as the amount allocated to each person is a multiple of two. Individual A may

not allocate any of the money to his- or herself. However, Individual A will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

A.2. Instructions for subjects in the Nationality treatment, taking the norm-elicitation task

first

Instructions

Welcome to this experiment. This is an experiment about decision-making. During the

experiment, we request that you remain quiet and do not attempt to communicate with other

participants. Participants not following this request may be asked to leave without receiving

payment. If you have any questions, please raise your hand and the experimenter will come to

you. For your participation, you will be paid a show-up fee of £4. You may also receive some

additional money based on your choices and the choices of others in the tasks described

below.

There will be two tasks for all participants to perform. At the end of the experiment, the

experimenter will toss a fair coin. If it lands on heads, all participants will receive payment

for the first task only; if it lands on tails, all participants will receive payment for the second

task only. As you will not know until the end of the experiment which task you will receive

payment for, please make your decisions in each task carefully. You will not receive feedback

on the outcome of any task until the end of the experiment, and your decisions in the first task

will have no effect on the nature or outcome of the second task. You will not receive any

instructions for or information about the second task until you have completed the first task.

After the second task, there will also be a questionnaire. The anonymity of your responses to

all parts of all tasks and questions is guaranteed.

Please now answer two questions on your screen, to ensure you understand the process of the

experiment.

In this experiment, the room has been divided into two sections on the basis of nationality. On

one side everyone is British; on the other side everyone is Chinese. The sign on your desk

reminds you whether you are on the British or Chinese side of the room.

108

Task One

In the first part of this experiment, you will receive a description of a situation. This

description corresponds to a situation in which one person, “Individual A,” must decide how

to act. You will be given a description of various possible actions Individual A can choose to

take.

After you receive the description of the situation, you will be asked to evaluate each of the

various possible actions Individual A can choose to take. You must indicate, for each of the

possible actions, whether taking that action would be "socially appropriate" or "socially

inappropriate". By socially appropriate, we mean behaviour that you think most participants

of your nationality would agree is the "correct" thing to do. Another way to think about what

we mean is that if Individual A were to select a socially inappropriate action, then another

participant of your nationality might be angry at Individual A.

In each of your responses, we would like you to answer as truthfully as possible, based on

your opinions of what constitutes socially appropriate or socially inappropriate behaviour.

To give you an idea of how the experiment will proceed, we will go through an example

situation and show you how you will indicate your responses.

Example Situation

Individual A is at a local coffee shop near campus. While there, Individual A notices that

someone has left a wallet at one of the tables. Individual A must decide what to do. Individual

A can choose four possible actions: take the wallet, ask others nearby if the wallet belongs to

them, leave the wallet where it is, or give the wallet to the shop manager.

The table below presents the list of the possible actions Individual A can choose. For each of

the actions, you would be asked to indicate whether you believe choosing that action is very

socially inappropriate, somewhat socially inappropriate, somewhat socially appropriate, or

very socially appropriate. To indicate your response, you would click on the corresponding

button.

109

If this was the situation for this study, you would consider each of the possible actions above

and, for that action, indicate the extent to which you believe taking that action would be

"socially appropriate" or "socially inappropriate". Recall that by socially appropriate we mean

behaviour that most participants of your nationality agree is the "correct" thing to do.

For example, suppose you thought that taking the wallet was very socially inappropriate,

asking others nearby if the wallet belongs to them was somewhat socially appropriate,

leaving the wallet where it is was somewhat socially inappropriate, and giving the wallet to

the shop manager was very socially appropriate. Then you would indicate your responses as

follows:

If you have any questions about this example situation or about how to indicate your

responses, please raise your hand now.

You will next be given the description of a situation where Individual A, a participant in an

experiment, has to choose between various possible actions. After you read the description,

you must consider the possible actions and indicate on your computer screen how socially

appropriate these are in a table similar to the one shown above for the example situation.

After this, the computer will randomly select one participant of your nationality (that is, it

will select a British participant if you are British, or a Chinese participant if you are Chinese).

The computer will then randomly select one action Individual A can choose. Your evaluation

of this action will be compared with that of the randomly selected participant of your

nationality. If your evaluation is the same as theirs, you will receive £8 for this task;

otherwise you will receive zero.

For instance, imagine the example situation above was the actual situation and the possible

action "Leave the wallet where it is" was selected by the computer. If your evaluation had

been "somewhat socially inappropriate" then your task earnings would be £8 if the person

you are matched with also evaluated the action as “somewhat socially inappropriate” and zero

otherwise.

The situation

110

Individual A is taking part in an experiment in this lab. The room has been divided into two

sections on the basis of nationality. On one side everyone is British; on the other side

everyone is Chinese. The anonymity of Individual A’s decisions in the experiment is

guaranteed.

Individual A’s task will be to decide how to divide £16 between two other participants in the

experiment, one who has the same nationality as Individual A, and another who has a

different nationality from Individual A. Individual A may divide the money any way he or she

likes so long as the amount allocated to each person is a multiple of two. Individual A may

not allocate any of the money to his- or herself. However, Individual A will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

Please now answer one question on your screen, to ensure you understand this situation.

111

Task Two

In this experiment, one third of you will be randomly assigned by the computer into a role

entitled ‘Individual A’. The decisions made by Individual As during the task will determine

the payments from the task received by the other two thirds of participants. Each of you has

an equal chance of being an Individual A. Exactly who the Individual As are will not be

revealed until the end of the experiment. In the meantime, we ask all participants to make a

decision as if they are an Individual A.

Please make your decision carefully, as it may be used to determine participants’ payments.

Assume for the rest of this paragraph that you are an Individual A. Your task is like the one

you evaluated in the previous task. Your task will be to decide how to divide £16 between two

other participants in the experiment, one who has the same nationality as you, and another

who has a different nationality from you. You may divide the money any way you like so

long as the amount allocated to each person is a multiple of two. You may not allocate any of

the money to yourself. However, you will also receive a payment. This payment might be £6,

£8 or £10. This will be randomly decided at the end of the experiment by the computer, which

is equally likely to select any of these amounts.

You will next see one question on your screen. Please answer it to ensure you understand this

part of the experiment.

A.3. Instructions for subjects in the Artificial treatment, playing the allocator game first

Instructions

Welcome to this experiment. This is an experiment about decision-making. During the

experiment, we request that you remain quiet and do not attempt to communicate with other

participants. Participants not following this request may be asked to leave without receiving

payment. If you have any questions, please raise your hand and the experimenter will come to

you. For your participation, you will be paid a show-up fee of £4. You may also receive some

additional money based on your choices and the choices of others in the tasks described

below.

There will be two tasks for all participants to perform. At the end of the experiment, the

experimenter will toss a fair coin. If it lands on heads, all participants will receive payment

for the first task only; if it lands on tails, all participants will receive payment for the second

task only. As you will not know until the end of the experiment which task you will receive

payment for, please make your decisions in each task carefully. You will not receive feedback

on the outcome of any task until the end of the experiment, and your decisions in the first task

will have no effect on the nature or outcome of the second task. You will not receive any

instructions for or information about the second task until you have completed the first task.

After the second task, there will also be a questionnaire. The anonymity of your responses to

all parts of all tasks and questions is guaranteed.

Please now answer two questions on your screen, to ensure you understand the process of the

experiment.

In this experiment, the room has been divided into two sections on the basis of which colour

of ball you drew from the bag at the beginning of the experiment. On one side everyone drew

112

a green ball; on the other side everyone drew a yellow ball. The sign on your desk reminds

you whether you are on the green or yellow side of the room.

113

Task One

In this experiment, one third of you will be randomly assigned by the computer into a role

entitled ‘Individual A’. The decisions made by Individual As during the task will determine

the payments from the task received by the other two thirds of participants. Each of you has

an equal chance of being an Individual A. Exactly who the Individual As are will not be

revealed until the end of the experiment. In the meantime, we ask all participants to make a

decision as if they are an Individual A.

Please make your decision carefully, as it may be used to determine participants’ payments.

Assume for the rest of this paragraph that you are an Individual A. Your task will be to decide

how to divide £16 between two other participants in the experiment, one who drew the same

ball colour as you, and another who drew a different ball colour from you. You may divide

the money any way you like so long as the amount allocated to each person is a multiple of

two. You may not allocate any of the money to yourself. However, you will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

Please now answer two questions on your screen, to ensure you understand this part of the

experiment.

114

Task Two

In the second part of this experiment, you will receive a description of a situation. This

description corresponds to a situation in which one person, “Individual A,” must decide how

to act. You will be given a description of various possible actions Individual A can choose to

take.

After you receive the description of the situation, you will be asked to evaluate each of the

various possible actions Individual A can choose to take. You must indicate, for each of the

possible actions, whether taking that action would be "socially appropriate" or "socially

inappropriate". By socially appropriate, we mean behaviour that you think most participants

who drew your ball colour would agree is the "correct" thing to do. Another way to think

about what we mean is that if Individual A were to select a socially inappropriate action, then

another participant who drew your ball colour might be angry at Individual A.

In each of your responses, we would like you to answer as truthfully as possible, based on

your opinions of what constitutes socially appropriate or socially inappropriate behaviour.

To give you an idea of how the experiment will proceed, we will go through an example

situation and show you how you will indicate your responses.

Example Situation

Individual A is at a local coffee shop near campus. While there, Individual A notices that

someone has left a wallet at one of the tables. Individual A must decide what to do. Individual

A can choose four possible actions: take the wallet, ask others nearby if the wallet belongs to

them, leave the wallet where it is, or give the wallet to the shop manager.

The table below presents the list of the possible actions Individual A can choose. For each of

the actions, you would be asked to indicate whether you believe choosing that action is very

socially inappropriate, somewhat socially inappropriate, somewhat socially appropriate, or

very socially appropriate. To indicate your response, you would click on the corresponding

button.

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If this was the situation for this study, you would consider each of the possible actions above

and, for that action, indicate the extent to which you believe taking that action would be

"socially appropriate" or "socially inappropriate". Recall that by socially appropriate we mean

behaviour that most participants who drew your ball colour agree is the "correct" thing to do.

For example, suppose you thought that taking the wallet was very socially inappropriate,

asking others nearby if the wallet belongs to them was somewhat socially appropriate,

leaving the wallet where it is was somewhat socially inappropriate, and giving the wallet to

the shop manager was very socially appropriate. Then you would indicate your responses as

follows:

If you have any questions about this example situation or about how to indicate your

responses, please raise your hand now.

You will next be given the description of a situation where Individual A, a participant in an

experiment, has to choose between various possible actions. After you read the description,

you must consider the possible actions and indicate on your computer screen how socially

appropriate these are in a table similar to the one shown above for the example situation.

After this, the computer will randomly select one participant who drew a ball of the same

colour as you (that is, it will select a participant who drew a green ball if you drew a green

ball, or a participant who drew a yellow ball if you drew a yellow ball). The computer will

then randomly select one action Individual A can choose. Your evaluation of this action will

be compared with that of the randomly selected participant who drew a ball of the same

colour as you. If your evaluation is the same as theirs, you will receive £8 for this task;

otherwise you will receive zero.

For instance, imagine the example situation above was the actual situation and the possible

action "Leave the wallet where it is" was selected by the computer. If your evaluation had

been "somewhat socially inappropriate" then your task earnings would be £8 if the person

you are matched with also evaluated the action as “somewhat socially inappropriate” and zero

otherwise.

The situation

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The situation you are asked to evaluate is like the one you participated in in the previous task.

Here is a summary.

Individual A is taking part in an experiment in this lab. The room has been divided into two

sections on the basis of which colour of ball participants drew from a bag at the beginning of

the experiment. On one side everyone drew a green ball; on the other side everyone drew a

yellow ball. The anonymity of Individual A’s decisions in the experiment is guaranteed.

Individual A’s task will be to decide how to divide £16 between two other participants in the

experiment, one who drew the same ball colour as Individual A, and another who drew a

different ball colour from Individual A. Individual A may divide the money any way he or she

likes so long as the amount allocated to each person is a multiple of two. Individual A may

not allocate any of the money to his- or herself. However, Individual A will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

A.4. Instructions for subjects in Artificial treatment, taking norm-elicitation task first

Instructions

Welcome to this experiment. This is an experiment about decision-making. During the

experiment, we request that you remain quiet and do not attempt to communicate with other

participants. Participants not following this request may be asked to leave without receiving

payment. If you have any questions, please raise your hand and the experimenter will come to

you. For your participation, you will be paid a show-up fee of £4. You may also receive some

additional money based on your choices and the choices of others in the tasks described

below.

There will be two tasks for all participants to perform. At the end of the experiment, the

experimenter will toss a fair coin. If it lands on heads, all participants will receive payment

for the first task only; if it lands on tails, all participants will receive payment for the second

task only. As you will not know until the end of the experiment which task you will receive

payment for, please make your decisions in each task carefully. You will not receive feedback

on the outcome of any task until the end of the experiment, and your decisions in the first task

will have no effect on the nature or outcome of the second task. You will not receive any

instructions for or information about the second task until you have completed the first task.

After the second task, there will also be a questionnaire. The anonymity of your responses to

all parts of all tasks and questions is guaranteed.

Please now answer two questions on your screen, to ensure you understand the process of the

experiment.

In this experiment, the room has been divided into two sections on the basis of which colour

of ball you drew from the bag at the beginning of the experiment. On one side everyone drew

a green ball; on the other side everyone drew a yellow ball. The sign on your desk reminds

you whether you are on the green or yellow side of the room.

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Task One

In the first part of this experiment, you will receive a description of a situation. This

description corresponds to a situation in which one person, “Individual A,” must decide how

to act. You will be given a description of various possible actions Individual A can choose to

take.

After you receive the description of the situation, you will be asked to evaluate each of the

various possible actions Individual A can choose to take. You must indicate, for each of the

possible actions, whether taking that action would be "socially appropriate" or "socially

inappropriate". By socially appropriate, we mean behaviour that you think most participants

who drew your ball colour would agree is the "correct" thing to do. Another way to think

about what we mean is that if Individual A were to select a socially inappropriate action, then

another participant who drew your ball colour might be angry at Individual A.

In each of your responses, we would like you to answer as truthfully as possible, based on

your opinions of what constitutes socially appropriate or socially inappropriate behaviour.

To give you an idea of how the experiment will proceed, we will go through an example

situation and show you how you will indicate your responses.

Example Situation

Individual A is at a local coffee shop near campus. While there, Individual A notices that

someone has left a wallet at one of the tables. Individual A must decide what to do. Individual

A can choose four possible actions: take the wallet, ask others nearby if the wallet belongs to

them, leave the wallet where it is, or give the wallet to the shop manager.

The table below presents the list of the possible actions Individual A can choose. For each of

the actions, you would be asked to indicate whether you believe choosing that action is very

socially inappropriate, somewhat socially inappropriate, somewhat socially appropriate, or

very socially appropriate. To indicate your response, you would click on the corresponding

button.

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If this was the situation for this study, you would consider each of the possible actions above

and, for that action, indicate the extent to which you believe taking that action would be

"socially appropriate" or "socially inappropriate". Recall that by socially appropriate we mean

behaviour that most participants who drew your ball colour agree is the "correct" thing to do.

For example, suppose you thought that taking the wallet was very socially inappropriate,

asking others nearby if the wallet belongs to them was somewhat socially appropriate,

leaving the wallet where it is was somewhat socially inappropriate, and giving the wallet to

the shop manager was very socially appropriate. Then you would indicate your responses as

follows:

If you have any questions about this example situation or about how to indicate your

responses, please raise your hand now.

You will next be given the description of a situation where Individual A, a participant in an

experiment, has to choose between various possible actions. After you read the description,

you must consider the possible actions and indicate on your computer screen how socially

appropriate these are in a table similar to the one shown above for the example situation.

After this, the computer will randomly select one participant who drew a ball of the same

colour as you (that is, it will select a participant who drew a green ball if you drew a green

ball, or a participant who drew a yellow ball if you drew a yellow ball). The computer will

then randomly select one action Individual A can choose. Your evaluation of this action will

be compared with that of the randomly selected participant who drew a ball of the same

colour as you. If your evaluation is the same as theirs, you will receive £8 for this task;

otherwise you will receive zero.

For instance, imagine the example situation above was the actual situation and the possible

action "Leave the wallet where it is" was selected by the computer. If your evaluation had

been "somewhat socially inappropriate" then your task earnings would be £8 if the person

you are matched with also evaluated the action as “somewhat socially inappropriate” and zero

otherwise.

The situation

119

Individual A is taking part in an experiment in this lab. The room has been divided into two

sections on the basis of which colour of ball participants drew from a bag at the beginning of

the experiment. On one side everyone drew a green ball; on the other side everyone drew a

yellow ball. The anonymity of Individual A’s decisions in the experiment is guaranteed.

Individual A’s task will be to decide how to divide £16 between two other participants in the

experiment, one who drew the same ball colour as Individual A, and another who drew a

different ball colour from Individual A. Individual A may divide the money any way he or she

likes so long as the amount allocated to each person is a multiple of two. Individual A may

not allocate any of the money to his- or herself. However, Individual A will also receive a

payment. This payment might be £6, £8 or £10. This will be randomly decided at the end of

the experiment by the computer, which is equally likely to select any of these amounts.

Please now answer one question on your screen, to ensure you understand this situation.

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Task Two

In this experiment, one third of you will be randomly assigned by the computer into a role

entitled ‘Individual A’. The decisions made by Individual As during the task will determine

the payments from the task received by the other two thirds of participants. Each of you has

an equal chance of being an Individual A. Exactly who the Individual As are will not be

revealed until the end of the experiment. In the meantime, we ask all participants to make a

decision as if they are an Individual A.

Please make your decision carefully, as it may be used to determine participants’ payments.

Assume for the rest of this paragraph that you are an Individual A. Your task is like the one

you evaluated in the previous task. Your task will be to decide how to divide £16 between two

other participants in the experiment, one who drew the same ball colour as you, and another

who drew a different ball colour from you. You may divide the money any way you like so

long as the amount allocated to each person is a multiple of two. You may not allocate any of

the money to yourself. However, you will also receive a payment. This payment might be £6,

£8 or £10. This will be randomly decided at the end of the experiment by the computer, which

is equally likely to select any of these amounts.

You will next see one question on your screen. Please answer it to ensure you understand this

part of the experiment.

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B: Photo of sign on desks in computer lab

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C: Analysis of the significance of ordering effects

In each of the Nationality and Artificial treatment we conducted three sessions (72

participants) wherein subjects first played the allocator game and then the Krupka-

Weber norm elicitation task, and two sessions (48 participants) where the order of

tasks was reversed. We test whether the order in which the tasks are played affects

either discrimination behaviour or the perceived appropriateness of discrimination.

Regarding the impact of task order on discrimination behaviour, randomisation tests

find the average level of observed discrimination does not significantly differ

between participants who play the allocation game first and those who have already

undergone the norm elicitation task, in either the Nationality treatment (p = 0.77) or

the Artificial treatment (p = 0.23). Regarding the impact of task order on the

perceptions of the appropriateness of discrimination, none of the evaluations are

subject to significant ordering effects in either the Nationality treatment (all p-values

> 0.229) or Artificial treatment (all p-values > 0.309). As in the main text, p-values

are corrected using the Benjamini-Hochberg false discovery rate procedure to account

for the fact that we are conducting multiple tests.

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D: Individual patterns of behaviour

We divide participants into five categories, on the basis of their responses to the

norm-elicitation task. Most individuals’ ratings monotonically increase in

appropriateness as allocations move away from the in-group favouring (16,0) towards

more equal allocations, until a peak is reached (usually the 8,8 split) after which the

individual’s ratings monotonically decrease in appropriateness. This means that the

individual believes the most appropriate possible action is not extreme discrimination.

We subdivide these participants into three types. UNBIASED types perceive

discrimination against the in-group member to be of equal appropriateness to

discrimination against the out-group member. IG-BIASED types perceive

discrimination against the in-group member to be of lesser appropriateness. OG-

BIASED types perceive discrimination against the out-group member to be of lesser

appropriateness. This categorisation is done by comparing the sum of the ratings the

individual assigns to in-group-favouring allocations against the sum of the ratings

they assign to out-group-favouring allocations.

Some participants, however, assign their highest rating to the (16,0) allocation and

then monotonically decrease the appropriateness of their ratings as more money is

given to the out-group member. Such participants are perceiving extreme

discrimination against the out-group member to be the social norm. We label them

PRO-DISCRIMINATORS. The few participants whose ratings do not follow any of

the above patterns are categorised as OTHER.

Figure D1 displays the percentage of participants in each treatment who followed

each pattern as well as their average levels of discrimination.

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Figure D1

Notes: Figure D1 shows the percentage of participants in each treatment whose

evaluations follow each pattern. Above each bar, D=the average level of

discrimination against out-group members by participants of the given type in the

given treatment – e.g. for UNBIASED participants in the Nationality treatment,

D=1.22 indicates these participants discriminated by an average of £1.22.

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E: Cross-national differences

We conclude with an analysis of cross-national differences in the perceptions of

appropriateness of discrimination as well as in discriminatory behaviour. Figure E1

compares, across nationalities, the mean evaluations of social appropriateness in each

treatment, while Tables E2a and E2b provide a full breakdown of responses, with

tests of significance. In both the Artificial and the Nationality treatment, Chinese

participants perceive discrimination to be more socially appropriate than British

participants. The general pattern of norms and most of the modal evaluations for a

given allocation is the same for the two nationalities. However, in both treatments all

in-group-favouring allocations are given significantly higher appropriateness ratings

by the Chinese. Out-group-favouring allocations are also perceived to be more

socially appropriate by the Chinese, but the difference is only significant for the

(6,10) split in Nationality. Finally, in both treatments, the equal split is given a lower

appropriateness rating by the Chinese, although the difference is significant only in

the Artificial treatment (p=0.028).

As the Chinese give relatively favourable evaluations to allocations favouring either

the in-group member or the out-group member, one might question whether what we

find is actually national differences in the social appropriateness of inequality rather

than of discrimination. However, note that the national differences in evaluations are

greater for in-group-favouring allocations than out-group-favouring ones. If the

national differences existed only for the social appropriateness of inequality, they

would be reflected in symmetrical national differences in the evaluation of in-group

and out-group favouring allocations.

In Table E3 we confirm this asymmetry is significant. We subtract the rating each

individual assigns to an allocation discriminating by a given amount in favour of the

out-group member from the rating they assign to the allocation which discriminates

by the same amount in favour of the in-group member. This provides a measure of the

relative appropriateness an individual ascribes to discriminating in favour of their

own group member rather than the other group member. We run randomisation tests

on these relative ratings for each level of discrimination, and find that in each case

there are significant national differences in the means. This indicates that, in both

treatments, the relative appropriateness of discriminating in favour of one’s own

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group member rather than the other group member is perceived to be significantly

higher by the Chinese than by the British.

Figure E1: Social appropriateness of allocations in the Nationality treatment

(left) and Artificial treatment (right)

Notes: Figure E1 shows the mean ratings participants of each nationality ascribe to

each allocation, in the Nationality treatment (left) and the Artificial treatment (right).

Mean ratings are constructed by assigning values of 1, 0.33, -0.33 and -1 for the

ratings ‘very appropriate’, ‘somewhat appropriate’, ‘somewhat inappropriate’ and

‘very inappropriate’ respectively, and averaging the values for all participants in a

given treatment. Allocations are denoted by the amount given to the in-group member

on the left, and the amount given to the out-group member on the right – e.g. (16,0)

denotes allocating £16 to the in-group member and £0 to the out-group member.

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Table E2a: Social appropriateness ratings of British and Chinese in Nationality

treatment

Allocation 16,0 14,2 12,4 10,6 8,8 6,10 4,12 2,14 0,16

British participants

v.appropriate 0.0 0.0 0.0 1.7 96.7 0.0 0.0 0.0 0.0

s.appropriate 0.0 0.0 3.3 33.3 1.7 26.7 3.3 1.7 1.7

s.inappropriate 1.7 15.0 41.7 38.3 1.7 41.7 36.7 10.0 1.7

v.inappropriate 98.3 85.0 55.0 26.7 0.0 31.7 60.0 88.3 96.7

Mean rating -0.99 -0.90 -0.68 -0.27 0.97 -0.37 -0.71 -0.91 -0.97

Chinese participants

v.appropriate 3.3 5.0 5.0 8.3 93.3 1.7 0.0 0.0 0.0

s.appropriate 6.7 11.7 16.7 70.0 5.0 43.3 5.0 1.7 1.7

s.inappropriate 3.3 25.0 53.3 18.3 1.7 45.0 51.7 20.0 1.7

v.inappropriate 86.7 58.3 25.0 3.3 0.0 10.0 43.3 78.3 96.7

Mean rating -0.82 -0.58 -0.32 0.22 0.95 -0.09 -0.59 -0.85 -0.97

p-value

(Benjamini-

Hochberg)

0.026 0.006 0.000 0.000 0.883 0.008 0.167 0.364 1.000

Table E2b: Social appropriateness ratings of British and Chinese in Artificial treatment

Allocation 16,0 14,2 12,4 10,6 8,8 6,10 4,12 2,14 0,16

British participants

v.appropriate 7.6 6.1 6.1 3.0 92.4 0.0 0.0 1.5 3.0

s.appropriate 0.0 1.5 3.0 53.0 4.6 40.9 6.1 1.5 0.0

s.inappropriate 0.0 12.1 50.0 31.8 1.5 42.2 43.9 12.1 0.0

v.inappropriate 92.4 80.3 40.9 12.1 1.5 16.7 50.0 84.9 97.0

Mean rating -0.85 -0.78 -0.51 -0.02 0.92 -0.17 -0.63 -0.87 -0.94

Chinese participants

v.appropriate 20.0 10.0 4.0 16.0 72.0 2.0 2.0 2.0 4.0

s.appropriate 12.0 20.0 36.0 78.0 18.0 52.0 6.0 2.0 0.0

s.inappropriate 0.0 24.0 48.0 4.0 6.0 36.0 50.0 18.0 0.0

v.inappropriate 68.0 46.0 12.0 2.0 4.0 10.0 42.0 78.0 96.0

Mean rating -0.44 -0.37 -0.12 0.39 0.72 -0.03 -0.55 -0.81 -0.92

P-value

(Benjamini-

Hochberg)

0.006 0.003 0.000 0.000 0.028 0.177 0.492 0.571 1.000

Notes: Tables E2a and E2b presents the breakdown, by percentage, of social appropriateness

ratings assigned to each allocation by participants of each nationality, in the Nationality

treatment (top) and Artificial treatment (bottom). Allocations (e.g. 16,0) are denoted by the

amount given to the in-group member on the left (£16), and the amount given to the out-

group member on the right (£0). Shaded cells represent the modal ratings for each allocation

in each treatment. Mean ratings are taken by assigning values of 1, 0.33, -0.33 and -1 for the

ratings ‘very appropriate’, ‘somewhat appropriate’, ‘somewhat inappropriate’ and ‘very

inappropriate’ respectively, and averaging the values for all participants in a given

treatment. Benjamini-Hochberg-corrected p-values are reported from randomisation tests on

the null hypothesis that the mean ratings on a given allocation are statistically

indistinguishable by nationality.

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Table E3: Appropriateness bias towards in-group favouritism over out-group

favouritism

Level of discrimination £16 £12 £8 £4

Nationality treatment

British -0.02 0.01 0.03 0.10

Chinese 0.15 0.27 0.27 0.31

p-Value (Bonferroni) 0.020 0.004 0.021 0.022

Artificial treatment

British 0.09 0.09 0.12 0.19

Chinese 0.48 0.44 0.43 0.42

p-Value (Bonferroni) 0.009 0.004 0.007 0.005

Notes: Table E3 shows the extent to which, on average, participants of each nationality

perceive discrimination by a given amount to be more appropriate when the beneficiary is the

in-group member, in the Nationality treatment (top) and the Artificial treatment (bottom).

The measure is constructed by subtracting each individual’s rating of an out-group-favouring

allocation from their rating of the equivalent in-group-favouring allocation. Benjamini-

Hochberg-corrected p-values are reported from randomisation tests on the null hypothesis

that the relative perceived appropriateness of discriminating in favour of an in-group

member rather than an out-group member does not differ between nationalities.

Finally, in Table E4 we look at whether the national differences in the perceived

social appropriateness of discrimination are reflected in more discriminatory choices

actually being made by the Chinese. In the Nationality treatment, the answer is no.

The distribution of allocations made by each nationality in this treatment is almost

identical. The mean difference between allocation to the in-group and out-group is

£1.27 by the British and £1.40 by the Chinese, amounts which are statistically

indistinguishable. However, in the Artificial treatment, the Chinese are more

discriminatory; 81.8% of British participants distribute the money equally compared

to only 52% of the Chinese, and the mean differences in allocations are significantly

different (p=0.007), at £1.88 and £4.72 for the British and Chinese participants

respectively. An OLS regression (Table E5) indicates that this finding is robust to the

inclusion of various controls.

Table E4: Discrimination in the allocator game – national comparisons

Allocation (16,0) (14,2) (12,4) (10,6) (8,8) (6,10) (4,12) (2,14) (0,16)

Nationality treatment

British 3.3 1.7 1.7 10.0 83.3 0.0 0.0 0.0 0.0

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Chinese 5.0 1.7 0.0 10.0 83.3 0.0 0.0 0.0 0.0

Artificial treatment

British 9.1 0.0 1.5 7.6 81.8 0.0 0.0 0.0 0.0

Chinese 18.0 6.0 4.0 20.0 52.0 0.0 0.0 0.0 0.0

Notes: Table E4 shows the percentage of participants of each nationality who choose each

allocation, in the Nationality treatment (top) and the Artificial treatment (bottom).

Allocations are denoted by the amount given to the in-group member on the left, and the

amount given to the out-group member on the right – e.g. (16,0) denotes allocating £16 to the

in-group member and £0 to the out-group member.

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Chapter Four: Nudging the electorate:

what works and why?56

Abstract

We report results from two studies designed to test the effectiveness of different

interventions to raise voter registration rates, and to probe the mechanisms underlying

observed behavior change. In the first study, in a natural field experiment ahead of the

2015 UK General Election, we varied the content of a postcard sent by Oxford City

Council to 7,679 unregistered student voters encouraging them to register onto the

electoral roll. We find that relative to a baseline condition, emphasising negative

monetary incentives (i.e. the possibility of being fined) significantly increases

registration rates, while positive monetary incentives (being entered into a lottery if

you register) may have some tendency to reduce registration rates. A third class of

purely non-monetary nudges have no overall effect on registration rates. In the second

study, we show that these differences can be explained, at least in part, by social

norms.

JEL classifications: D72: Political Processes: Rent-Seeking, Lobbying, Elections,

Legislatures, and Voting Behavior; D03: Behavioral Microeconomics: Underlying

Principles; C93: Field Experiments; H83: Public Administration.

Keywords: Voter Registration; Voting; Field Experiment; Nudging; Social Norms;

Fines; Rewards.

56 This chapter was co-authored with Felix Kölle, Daniele Nosenzo and Chris Starmer

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1. Introduction

Behavioural science is increasingly being used to advance low-cost interventions

across a growing spectrum of public policy areas. The associated body of research is

being built by – and is of interest to – both academics (e.g. Chetty, 2015; Hallsworth

et al., 2014) and applied policy units (e.g. Behavioural Insights Team, 2010, 2011,

2012, 2016). Interventions often take the form of ‘nudges’ – manipulations of the

‘choice architecture’ which aim to systematically change people’s behaviour at low

cost for the policymaker.57 This paper explores aspects of the mechanics of nudging

by using a combination of field and online experiments. Our natural field experiment

explores the extent to which a particular decision can be influenced by different types

of nudge; with our online experiment we investigate the underlying mechanisms that

lead to the success or failure of different nudges.

We do this in the context of a particular policy area: voter registration. In many

countries – including the United Kingdom, where our study is conducted – any citizen

wishing to vote must first register on the electoral roll. Registration in the UK is

technically mandatory, with non-registration punishable with an £80 fine, although in

the past two decades a substantial gap has emerged between the numbers of eligible

and registered voters (Bite the Ballot, 2016), one which was further increased by the

implementation of a legislative change in 2014: previously all members of a

household could be registered collectively, but the law now requires each person to

register individually (Electoral Registration and Administration Act 2013). Besides

any intrinsic benefits of wide democratic participation, high registration rates serve

the government’s interest insofar as the electoral roll has secondary uses such as

fraud-detection and jury recruitment. Given its very low cost nature, nudging – if it

can be shown to be effective – would be an attractive strategy for such organisations

to employ in pursuit of this goal. Our study therefore explores interventions that can

57 We are using the label ‘nudge’ to describe any type of low-cost intervention that is designed with

the objective of changing individuals’ behaviour. Thaler and Sunstein (2008) refer to ‘nudges’ to

describe interventions that leave unaffected the underlying economic incentives: some of the

manipulations that we use in our experiment have this property, whereas others induce small

changes in the underlying incentives and so, strictly speaking, would not qualify as nudges

according to the Thaler and Sunstein’s definition.

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be applied, at minimal financial expense, to nudge citizens to register to vote in

elections.

In the first part of this paper, we report the results of a natural field experiment run

ahead of the 2015 UK General Election in partnership with one such interested party,

Oxford City Council, who sent postcards to students living in university

accommodation, encouraging them to register. Councils have a particular interest in

discovering successful ways of targeting such students, as they represent a segment of

society whose registration rates have been particularly affected by the recent legal

change – previously universities could register en masse all accommodated students,

but students are now required to register themselves individually. While all the

postcards urged recipients not to miss their chance to vote, we systematically varied

the precise content of their messages in order to test the effects of different nudges on

registration rates.

We investigated two broad types of nudges, relying on monetary incentives in the

form of either a small gain or a small loss. There is a large and diverse literature in

economics showing that interventions based on negative incentives, such as the threat

of monetary loss, may produce stronger responses than those relying on positive

incentives, such as the promise of monetary gains, even when the interventions

involve identical financial incentives and the only difference is in the way these

incentives are described to the individual (for reviews of these literatures, see, e.g.,

Balliet et al., 2011; van Lange et al., 2014; Nosenzo, 2016). In the context of policy

interventions aimed at reinforcing civic duties, as in the case of voter registration,

positive and negative incentives may produce different behaviours because of the way

they interact with the very notion of 'civic duty': while negative incentives may

reinforce the perception that registering to vote is what one ought to do, positive

incentives may have the opposite effect. In the second part of our paper, we

investigate this hypothesis by examining the effects that positive and negative

incentives have on the perception that registering to vote is a normative obligation.

We also investigated another class of nudges, which do not involve financial

incentives but rely on purely psychological mechanisms to affect behaviour. We refer

to these as our non-monetary nudges. Non-monetary nudges are sometimes regarded

133

as preferable to monetary ones, especially in areas of public policy, such as voter

registration programs, where intrinsic motivations may play an important role in

producing the desired behaviour: the concern here is that the use of extrinsic

(monetary) incentives may crowd-out these intrinsic motivations (see, e.g., Gneezy et

al., 2011; Bowles and Polania-Reyes, 2012). Another advantage of non-monetary

interventions, compared to monetary ones, is that the former typically involve smaller

financial costs than the latter.

In our field experiment, we implement these nudges across six treatments. In a

baseline treatment, the postcard that was sent to unregistered student voters simply

encouraged them to register, without any additional message. We investigate the

effectiveness of monetary losses in a second treatment by adding a message

highlighting the existence of the potential £80 fine for those who fail to register.

Emphasising the possibility of encountering financially costly legal action has

previously been found to exert a substantial positive effect in other domains of policy

intervention, such as the enforcement of TV license registration (Fellner et al., 2013),

credit card debt repayment (Bursztyn et al., 2015), or traffic violations (Lu et al.,

2016).58 Kleven et al. (2011) similarly found that the threat of audits raised tax

returns, although mixed evidence was found in this domain by Blumenthal et al.

(2001) and Slemrod et al. (2001).59

To test the effectiveness of monetary gains, we designed two further treatments where

students were offered entry into a lottery to win small cash prizes (of the value of

£80) for those who registered early. Financial inducements have previously been

found to raise voter registration (John et al., 2015) and voter turnout (Panagopoulos,

2013), although in the latter case only when the inducements were sufficiently large.

Moreover, in John et al. (2015) the lottery involved large financial incentives

(between £1000 and £5000) and produced only a small positive effect (an increase of

two percentage points in registration rates).

58 However, Lu et al. (2016) found that messages were effective only when they contained

personalised information about own past traffic violations, and not when they communicated the

mere existence of fines.

59 See Hallsworth (2014) for a recent review of field experiments on tax compliance interventions.

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Finally, we investigate the effectiveness of non-monetary nudges in two treatments

where we included in the postcard messages that invoked purely psychological

mechanisms. Specifically, we attempted to harness the so called ‘foot-in-the-door’

mechanism. First identified by Freedman and Fraser (1966), this is a psychological

effect – which has been replicated across a wide array of circumstances (see e.g.

Burger, 1999) – wherein people are more likely to comply with a large request,

oriented towards a particular goal, after they have first complied with a small request.

In our case, the small requests took the form of asking students to provide their phone

number (so that they could be sent a reminder to register); or simply to report by text

whether they intended to register.

Our results show that emphasising the possibility of being fined yielded a large

positive effect, with subjects exposed to this intervention being around 1.7 times more

likely to register than those exposed to the baseline intervention. In contrast, the

prospect of financial gain had no overall effect on registration – and once the deadline

for entry into the lottery had passed, subjects exposed to this intervention were

significantly less likely to register than those in the baseline condition. Meanwhile,

the non-monetary interventions had no discernible effect.

In the second part of the study reported in this paper, we investigated a possible

mechanism underlying the effectiveness of the negative monetary incentives and the

ineffectiveness of positive incentives: their contrasting effects on the perception of

what constitutes socially appropriate behaviour in the context of voter registration. A

growing body of recent economic research (e.g., Burks and Krupka, 2012; Gächter et

al., 2013; Krupka and Weber, 2013; Banerjee, 2016; Barr et al., 2016; Krupka et al.,

2016) suggests that social norms and norm-compliance drive behaviour in a wide

range of contexts. We hypothesised that the fine and lottery treatments may have

divergent effects on the perceptions of normative appropriateness of registering to

vote: emphasising that failing to register is punishable by law may strengthen the

perception that one ought to register, while offering monetary inducements for

registering may weaken the perception that doing so is an action already expected

within society.

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Our results support these hypotheses. Using the incentivised norm-elicitation method

introduced by Krupka and Weber (2013), we found that exposing individuals to the

fine nudge strengthened their perception that failing to register to vote was socially

inappropriate behaviour, while exposing them to the lottery nudge weakened the

perception that registering to vote was socially appropriate behaviour. Consequently,

we propose that strengthening/weakening the social norm relating to registration had

a direct effect on respondents’ likelihood of registering, and that this partly explains

why the fine intervention was successful while the lottery intervention was not.

Indeed, a possible interpretation of our results is that– just as in some previous

research (e.g. Frey and Oberholzer-Gee, 1997; Ariely et al., 2009; Gneezy et al.,

2011; Bowles and Polania-Reyes, 2012) – the introduction of monetary incentives

crowded out individuals’ intrinsic motivation to engage in socially constructive

behaviour (especially once the deadline for the lottery had passed), and the adverse

effect of the lottery intervention on the perceived social norm of registering may be

partly behind this effect.

Our study contributes to the literature regarding behavioural insights and nudging in

public policy. We identify a low-cost strategy – emphasising the possibility of a fine

for not registering – that governments can use to substantially increase registrations.

However, we also identify cases where nudges can fail to work or perhaps even

backfire. We show offering monetary rewards for registering can have neutral or

adverse effects, while attempting purely psychological interventions may not yield

any desired positive effects. One advantage of our study is that our investigation into

the relative effectiveness of non-monetary and monetary nudges (and, within the

latter, of positive and negative incentives) is done within a unified experimental

design and in the context of a large-scale field intervention (N = 7,679).

Moreover, another distinctive feature of our paper is that our focus is not only on

identifying which intervention is most effective to encourage voter registration, but

also on understanding the underlying behavioural and psychological mechanisms that

make specific interventions more successful than others. In particular, we believe that

we are the first to show that policy interventions that rely on positive incentives may

weaken, whereas those relying on negative incentives strengthen, the perceptions of

normative appropriateness of the target behaviour. These differences in normative

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perceptions may explain the relative success of the positive and negative monetary

interventions that we found in our field experiment. In this sense, our paper also adds

to the recent economic literature on the importance of social norms for understanding

human social behaviour (Krupka and Weber, 2013; Gächter et al., 2013; Kimbrough

and Vostroknutov, 2016).

2. Study I: Field experiment on voter registration

2.1 Experimental design

Our field experiment was designed to test the effectiveness of six different low cost,

nudge-style, interventions for raising voter registration rates ahead of the 2015 UK

General Election. These six interventions fall into three broad categories: negative

monetary nudges; positive monetary nudges; and non-monetary nudges. All of these

interventions were implemented via adjustments to a message sent in a bulk,

randomised, mail out (details below) to students living in the UK City of Oxford.

We implemented one negative monetary intervention invoking the threat of a

monetary loss for failing to register. We did this by highlighting to subjects the

truthful fact that they could be fined £80 if they did not register. This penalty is

specified in UK law, and it is referred to in standard materials that Oxford City

Council (OCC) use to promote voter registration. Despite the power existing in law,

however, it is rarely used by councils and it is unclear how aware a typical

unregistered voter would be of the possibility of being fined for failure to register.

We implemented two interventions involving the prospect of monetary gain for

registering. We did this with two treatments offering entry into a lottery to win cash

prizes of the value of £80 for those who registered by a specific deadline. The two

treatments differed only in that one attempted also to harness regret aversion (Loomes

and Sugden, 1982), by telling recipients that those who did not register would still be

entered into the lottery and informed if they won, but would be unable to claim their

prize. Regret aversion has previously been shown to affect entry decisions into

lotteries (Zeelenberg and Pieters, 2004; Gneezy, 2014; Imas et al., 2016).

137

We also implemented two interventions involving non-monetary mechanisms.60, 61

These were motivated by the so called foot-in-the-door effect (Freedman and Fraser,

1966). More specifically, we tested whether message recipients were more likely to

register (i.e., comply with a large request) if they had first complied with a small

request related to voter registration: in both variants, subjects were asked to send a

one-word text message to OCC; in one case subjects were asked to text the word

‘myvote’ to indicate that they planned to register; in the other, subjects could text the

word ‘reminder’ to register to receive a free reminder text to prompt them to register

nearer the deadline for voters to register in the 2015 UK General Election.62 Foot-in-

the-door mechanisms have previously been tested in the context of voter turnout, with

mixed results: asking subjects if they intended to vote was found to have a large,

positive impact on turnout by Greenwald et al. (1987, 1988), but not by Smith et al.

(2003).

Our nudges were transmitted via postcards, which OCC mailed to all unregistered

voters living in student accommodation belonging to the University of Oxford and

Oxford Brookes University on March 9-10 2015, ahead of the April 20 deadline for

60 There are a number of non-monetary interventions that have been shown to positively affect voter

turnout, e.g. personalised get-out-the-vote contact (e.g. Gerber and Green, 2000; Ramirez, 2005),

priming one’s identity as a voter (Bryan et al., 2011), or applying social pressure on people to vote

(e.g. Gerber et al., 2008, 2010; Davenport, 2010; Panagopoulos, 2010). See Rogers et al. (2013) for

a recent review of this literature. While one might expect that what works for voter turnout should

also work for voter registration, ultimately this is an empirical question. Nevertheless, the fact that

voter turnout appears quite susceptible to psychological processes provides a strong motive for

exploring non-monetary nudges as a policy tool regarding registration.

61 We also considered designing a ‘peer pressure’ treatment, where we would inform students of the

past registration rates of their peers in order to induce them to register. However, at the time we

designed the experiment, the registration rate of students was very low (about 8-9%) and we

thought that informing subjects of such low rates may actually have the opposite effect of

discouraging registrations.

62 Our primary interest in relation to this treatment was in assessing whether the act of registering for

an automated text reminder (which was designed to be very quick and easy) would act as a foot in

the door, enhancing the propensity to subsequently register to vote. We were not especially

interested in the later effect that a subsequent automated reminder might have (we do not have

controlled comparisons for benchmarking any such effect). Of course all of our treatments can be

considered as sending slightly different forms of reminder and, more broadly, reminders have

been shown to be effective nudges in relation to voter registration (Bennion and Nickerson, 2011),

as well as in other contexts (e.g. Altmann and Traxler, 2014)

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voters to register in the General Election. We collaborated with the Council to

engineer the content of these postcards. While all postcards encouraged their

recipients to register, the content of the messages they contained varied, allowing us

to test the effects of different nudges on registration rates.

All postcards were double sided (see Figure 1 for a copy of the postcard used in our

baseline condition and Appendix A for copies of the other postcards). The back

simply contained the message, ‘IMPORTANT INFORMATION ABOUT YOUR

RIGHT TO VOTE, OVERLEAF.’ The front featured the heading, ‘DON’T MISS

YOUR CHANCE TO VOTE! According to our records you have not yet registered to

vote. It’s easy to register online. To go to the registration page simply use one of the

links below.’ The bottom of this side contained the address of the government web

page for registering to vote, and a QR code which would take recipients to the same

page. These features were held constant across treatments. The postcards differed by

treatment only according to the text included in a box below the heading on the front

side.

Figure 1: Postcard used in the Baseline treatment

2.2 Treatments

In the Baseline treatment, the box was left blank (Figure 1). This treatment therefore

serves as a basis for comparison against the other treatments.

139

In the Monetary Loss treatment, the box contained the message: ‘If you don’t

register you could be fined £80.’.

In treatment Monetary Gain 1, the box contained the message: ‘If you register by 27

March 2015 you will be entered into a lottery to receive one of ten £80 prizes.

Winning students will be notified in June 2015.’. In treatment Monetary Gain 2, the

box contained the message: ‘You have been entered into a lottery to receive one of ten

£80 prizes. Winners will be notified in June 2015 but you will only be able to claim

your prize if you were already registered by 27 March 2015. If not your prize will go

to another student.’.

In treatment Non-Monetary 1, the box contained the message: ‘We’d like to know if

you are intending to register. If you are, please text ‘myvote’ to 60886.’. In treatment

Non-Monetary 2, the box contained the message: ‘Would you like us to send you a

text reminder? If you do, please text ‘reminder’ to 60886.’. In both cases, texts were

free of charge and this was clearly stated in the postcard.

2.3 Assignment to treatment

The postcards were sent out on March 9-10 2015 to 7,679 voters who were still

unregistered at the time and who lived in student accommodation buildings belonging

to the University of Oxford and Oxford Brookes. In order to minimise the likelihood

of subjects seeing postcards belonging to treatments other than the one they were

assigned to, we randomised assignment to treatment at the building level: all students

living in a single building were assigned to the same treatment. For the University of

Oxford, all students living in a single college were assigned to the same treatment.

For Oxford Brookes University, all students living in a single hall of residence were

assigned to the same treatment, with the exception that two very large halls were split

into several geographically distinct units of assignment. This was to ensure balance

between treatments in the proportion of subjects attending each university – we

considered this important, given large demographic (in particular, socioeconomic)

differences between the student populations of each university. We further balanced

treatment assignment by residence size (small and large) and to the age of college

(ancient and modern) to account for other potential unobserved characteristics. The

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resulting sample sizes were as follows: Baseline (n = 1193); Monetary Loss (n =

1357); Monetary Gain 1 (n = 1250); Monetary Gain 2 (n = 1317); Non-Monetary 1 (n

= 1262); and Non-Monetary 2 (n = 1300). See Appendix B for further details on the

assignment procedure and for a full breakdown of the colleges and halls assigned to

each treatment.

2.4 The dataset

OCC provided us with anonymised data on registration rates amongst students

residing in each college and hall at various points in time between January and April

2015. In particular, for each individual in our dataset, our data specify whether or not

they were registered on: January 2, March 8 (the day before the postcards of our

experiment were sent out), and any subsequent day between March 9 and April 20

(the formal deadline to register to vote for the General Election). The data also

contain information on the treatment each individual was assigned to, their university

affiliation (University of Oxford or Oxford Brookes University), and their hall or

college. Other demographic data such as gender, age, etc. was not available to the

Council.

3. Results

In the following analysis we pool data from the two Monetary Gain treatments. This

is because we found there were no significant differences between the effects of

Monetary Gain 1 and Monetary Gain 2 (see Table C1 in the Appendix). Similarly, we

found no significant differences between the two Non-Monetary treatments (see

Table C1) and thus, for ease of exposition, we combine these two treatments in our

analysis. Thus, in the remainder of the section, our analysis is based on the following

four conditions: Baseline (n = 1193); Monetary Loss (n = 1357); Monetary Gain (n =

2567); and Non-Monetary (n = 2562).

Figure 2 shows how registration rates differ between treatments over the entire period

between the intervention and the deadline for registering. On a daily basis between

March 8 and April 20, it displays the cumulative fraction, by treatment, of registered

subjects amongst those who were unregistered on January 2.

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Figure 2: Cumulative registration rates by treatment

Notes: Figure 2 shows, on a daily basis between March 8 and April 20, the amount of

registered students in the treated buildings as a fraction of all students in these

buildings who had been unregistered on January 2. The first vertical line represents

the day of our treatment intervention (March 9) and the second line represents the day

of the lottery deadline in the Monetary Gain treatments (March 27).

Pre-intervention registration rates (i.e. in the period January 2 – March 8) are very

similar across all treatments; the fraction of registered subjects ranges between 0.080

and 0.088, showing no significant differences across treatments (see also Table 1

below). This suggests that later treatment differences are unlikely to be driven by pre-

existing differences between the subjects assigned to each intervention.

After our intervention (i.e. in the period March 9 – April 20), substantial differences

emerge in the registration rates across treatments. On April 20 (the day of the

registration deadline), the fraction of registered students amounts to 0.25 in Baseline,

0.31 in Monetary Loss, 0.21 in Monetary Gain, and 0.25 in the Non-Monetary

treatment. Hence, compared to the case of a simple postcard, only the emphasis of

(potential) negative monetary consequences had a positive effect on registration;

registration rates in Monetary Loss are 24% higher than in Baseline. The emphasis of

(potential) positive monetary consequences, in contrast, had no positive effect on

registration rates. While registration rates are initially somewhat above the ones in

Treatmentintervention

Lotterydeadline

0

.05

.1

.15

.2

.25

.3

.35

Reg

istr

ation

ra

te

-1 1 5 9 13 17 21 25 29 33 37 41

Days since intervention

Baseline

Monetary Loss

Monetary Gain

Non-Monetary

142

Baseline, this effect flips towards the end of our observation period, after monetary

incentives have been removed again. Overall, the registration rate in our Monetary

Gain treatments is 16% lower than in Baseline. For the Non-Monetary treatments, we

find almost identical registration rates as in Baseline, suggesting that the effects of the

non-monetary nudges were minimal in our setup. Given how few engaged with the

invitation to send a text message (only 4 students requested a text reminder, while a

mere 9 texted their intention to register) it is not surprising that we record no

discernible foot-in-the-door effect.

To further explore the observed treatment differences in registration rates, we run

logistic regressions to model the individual level registration decision. Our dependent

variable is 1 or 0 depending on whether or not an individual has registered in a given

period. As independent variables, we use dummies to represent the treatment an

individual was assigned to. Given the very different nature of the two universities that

were included in our study, we also include a dummy variable for whether a student

was affiliated with either Oxford Brookes University or University of Oxford. As

further controls we include: which of the two Oxford voting areas (General Election

constituencies) a given student resides in; the size of the residence unit they live in;

and an ‘ancient’ dummy, which takes value 1 if the college or hall in which they live

is older than 100 years, and value 0 otherwise.63 To correct for heteroscedasticity and

potential dependency of observations within halls, we cluster standard errors by

residence unit.64 The results of these regressions are reported in Table 1.

Model (1) reports, for each treatment relative to Baseline (the omitted category), the

factor changes in the odds of registering in the period before our intervention (i.e.

between January 2 and March 8). The sample includes all students in treated

buildings who were unregistered on January 2. In the Baseline treatment, the odds of

registering in the pre-intervention period are 0.174, i.e. there are expected to be

approximately 6 unregistered students for each registered student in our benchmark

63 We included this dummy because we conjectured that there could be some difference in ethos or

culture which could be relevant to the registration decision, comparing older and more newly

established colleges.

64 That is, each college, hall, residence block, and/or cross-college accommodation is treated as

providing a cluster of observations (see Appendix B for further details).

143

condition. The odds of registering are very similar in the other treatments: in all cases

the factor changes in the odds are close to 1 and none of the treatment variables are

significant (all p-values > 0.532). This confirms that registration rates are

indistinguishable across treatments in the pre-intervention period.

Table 1: The effects of treatments on registration rates

Dependent variable Registered (1 if yes, 0 otherwise)

(1) (2)

Before

Intervention

(Jan 2 – Mar 8)

After

Intervention

(Mar 9 – Apr 20)

Monetary Loss 0.968 1.739***

(0.250) (0.348)

Monetary Gain 1.123 0.749

(0.209) (0.171)

Non-Monetary 0.930 1.009

(0.195) (0.180)

Odds of registering in Baseline 0.174*** 0.250***

(0.064) (0.072)

Controls Yes Yes

N 8397 7679

Notes: The table reports odds ratios from logistic regressions. Note that a ratio greater than 1 implies a

positive effect, whereas a ratio smaller than 1 implies a negative effect. The dependent variable

indicates whether an individual registered within a given period. Robust standard errors clustered at the

residence unit are reported in parentheses. Significance levels: *** p<0.01, ** p<0.05, * p<0.1

In model (2), we look at the effect of our different nudges after their implementation.

The dependent variable now is whether an individual registered or not during the

period between March 9 and April 20, the day of the registration deadline. The

sample includes all students in treated buildings who were still unregistered on March

8 (i.e., we drop those who registered before the intervention, since they did not

receive the postcards that were sent out on March 9). The treatment dummies

therefore represent treatment differences in registration rates after the intervention.

The odds of registering in Baseline are now 0.25: there are expected to be 4

unregistered students for each registered student in Baseline. The higher odds of

registering in the post-intervention period relative to the pre-intervention period may

144

reflect an impact of sending the postcard per se, or a natural increasing trend in

registrations as the deadline for the General Election draws nearer.65

The Monetary Loss treatment increases the Baseline odds by a factor of 1.7 and the

effect is significant at the 1% level. This implies an expected ratio of almost 2:1

between unregistered and registered students in the Monetary Loss treatment (the

odds of registering are 0.25 x 1.739 = 0.43). In contrast, the Monetary Gain treatment

reduces the odds of registering relative to Baseline by a factor of 0.749, although the

effect does not reach statistical significance (p = 0.205). The Non-Monetary treatment

has virtually no impact on the odds of registering, with a factor change close to 1 and

very far from statistical significance (p = 0.958).66

Another interesting feature of the effect of the Monetary Gain Treatments is apparent

in Figure 2. While at the beginning registration rates under the Monetary Gain

treatments are very similar to the ones in Baseline, in the former they experience a

less pronounced uptick towards the end of the post-intervention period, after the

deadline for eligibility to enter the lottery has passed (on March 27).

To quantify the negative post-deadline effect of the Monetary Gain treatments, we

split our data into two time periods. The first period spans from the day of our

intervention until the lottery deadline (i.e. between March 8 and March 27). The

second period starts from the first day after the lottery deadline until the registration

deadline (i.e. between March 28 and April 20). As before, we apply logistic

regression analysis. Note that we only use data from Baseline and Monetary Gain

treatments, as the March 27 deadline is inconsequential in the other treatments. The

results of this analysis are presented in Table 2. Model (1) reports the factor changes

in the odds of registering in Monetary Gain relative to Baseline in the first period.

The sample includes all students in treated buildings who were unregistered on March

8. In Model (2), we instead only look at the period after the deadline for the lottery

65 We cannot distinguish between these two explanations because, in designing our treatments in

collaboration with OCC, we agreed not to have a treatment where no postcard was sent.

66 To test the robustness of these results, for the post-intervention period we also apply duration

analysis to examine the time it takes an individual to register after having received our postcards.

The results of the duration analysis are consistent with those of the logistic regressions, as we

show in Appendix C, Table C2 (model (1)).

145

has passed already. The sample now includes all students in treated buildings who

were still unregistered on March 28, i.e., we drop those subjects who registered

before the lottery deadline. As before, we cluster standard errors by unit of residence..

Table 2: The effect of the lottery deadline on registrations relative to Baseline

Dependent variable:

Registered (1 if yes, 0 otherwise)

(1) (2)

Before

Deadline

(Mar 8– Mar 27)

After

Deadline

(Mar 28 – Apr 20)

Monetary Gain 1.286 0.657*

(0.463) (0.425)

Monetary Gain x Post deadline

Odds of registering in Baseline 0.070*** 0.096***

(0.047) (0.026)

Controls Yes Yes

N 3760 3579

Notes: The table reports odds ratios from logistic regressions. Note that a ratio greater than 1 implies a

positive effect, whereas a ratio smaller than 1 implies a negative effect. The dependent variable indicates

whether an individual registered within a given period. Only data from Monetary Gain and Baseline are

included. Robust standard errors clustered at the hall level are in parentheses. Significance levels: ***

p<0.01, ** p<0.05, * p<0.1

The results of model (1) reveal that before the end of the lottery deadline being

subject to the Monetary Gain treatment slightly increases the odds of registering

relative to being subject to the Baseline treatment, by a factor of 1.286, but the effect

does not reach statistical significance (p = 0.485). In contrast, once the deadline for

the lottery has passed, i.e., monetary incentives for registering have been removed

again, being subject to the Monetary Gain treatment reduces the odds of registering

relative to being subject to the Baseline treatment by a factor of 0.657, and this effect

is statistically significant (p = 0.057).67 This suggests that implementing monetary

incentives has no positive effect while in place, but removing the monetary incentives

67 To test the robustness of this result, we again use duration analysis. As we show in Appendix C,

Table C2 (model (2)), the result of the duration analysis is consistent with that of the logistic

regression analysis.

146

afterwards has a negative effect on registration rates. This would be in line with the

literature on motivational crowding out (e.g. Deci And Ryan, 1985; Frey and

Oberholzer-Gee, 1997; Meier, 2007), However, it is also possible that the low post-

deadline registration rate amongst subjects in the Monetary Gain treatments, relative

to those in Baseline, was the result of individuals who otherwise would have

registered during this period having been motivated by the lottery to already register

before the deadline passed.

To summarise our main findings so far, we find that emphasising the possibility of

being fined significantly raises registration rates, while attempting to invoke the foot-

in-the-door effect makes no significant impact. Furthermore, using positive monetary

incentives may actually backfire and even lower registration rates, especially after the

incentives are removed.

4. Study II: The effects of the monetary nudges on social norms

The main finding of our field experiment is that the threat of a monetary fine is more

effective in encouraging registrations than the chance of a monetary gain (which has

initially no effect and later, once the possibility of gain is removed, a negative effect),

or foot-in-the-door type interventions (which have no effect). There are a number of

possible mechanisms that could explain why the threat of a fine is more effective than

the chance of a gain overall (e.g., loss aversion; or a bias in beliefs whereby

individuals assess the probability of being fined as higher than the probability of

winning the lottery). While we do not rule out such mechanisms being at work in our

data, other explanations would be required for how the offer of a monetary gain in the

form of a lottery could have a negative effect on registration, even compared to

Baseline. In this section, we explore a possible explanation that might organize the

contrasting impacts of money gains and money losses in our design. Specifically, we

investigate the potentially different effect of these interventions on social norms, i.e.

collectively recognised rules of behaviour that define which actions are viewed as

socially appropriate (Elster, 1989; Ostrom, 2000). We considered this to be a

promising channel to pursue because, as we now explain, there are plausible and

contrasting effects that our fine and lottery nudges could have had on the perceived

social appropriateness of registration behaviour.

147

We conjecture that the Monetary Loss treatment may strengthen a pre-existing social

norm that registering to vote is what one ought to do: emphasising that failing to

register is against the law may solidify one’s perception that such behaviour is

socially inappropriate.68 In contrast, the Monetary Gain treatments may weaken that

same social norm – the offer of money for registering may suggest to recipients that

registering is not something already unconditionally demanded of them by society. If

social norms influence registration behaviour, such alterations of subjects’

perceptions of them could directly affect their decisions over registration. Indeed, the

failure of the Monetary Gain treatments is reminiscent of previous research showing

the introduction of economic incentives can crowd out people’s intrinsic motivation

to behave pro-socially (e.g. Frey and Oberholzer-Gee, 1997; Ariely et al., 2009;

Gneezy et al., 2011; Bowles and Polania-Reyes, 2012). A plausible mechanism

behind the offer of financial reward crowding out intrinsic motivation to register

could be the lottery’s weakening effect on the social norm of registering.

4.1 Experimental design and procedures

To investigate this, we ran an online study, employing the social norm elicitation task

pioneered by Krupka and Weber (2013). In this study, we first described to subjects

the setting of our field experiment. We then exposed each subject to the postcard used

in one of three treatments – Baseline, Monetary Loss and Monetary Gain 169 – and in

each case measured the social norms they perceived pertaining to registration

behaviour.

This study was run in June 2016, with subjects who were students at the University of

Nottingham, recruited through ORSEE (Greiner, 2015), an online database of

68 There is some debate over whether social norms and laws are substitutes, or whether laws directly

shape norms. See, for instance, Posner (2009) and Benabou and Tirole (2011).

69 We chose to focus only on the Monetary Loss and Gain treatments because in the field experiment

the monetary interventions produced the most interesting effects on registration rates relative to

Baseline. The Non-Monetary treatments had no significant effects on registration rates and were

indeed highly ineffective in engaging subjects. We only focus on one version of the Monetary Gain

treatments because in the field experiment the Monetary Gain 2 treatment was statistically

indistinguishable from Monetary Gain 1 and we thought that Monetary Gain 1 was easier to

describe to subjects.

148

experimental participants. Thus, the subjects would have been demographically

similar to those in the field experiment, but would not have been previously exposed

to the postcards. In total 189 subjects participated in the study: 65 were shown the

Baseline postcard, 61 the Monetary Loss postcard, and 63 the Monetary Gain 1

postcard. The study was conducted using Qualtrics (Qualtrics, 2016), an online

survey platform.

At the beginning of the experiment, subjects were told to ‘Imagine that the date is

March 8, 2015. There is an upcoming General Election on May 7, and a local council

wants to encourage people to register to vote before the deadline on April 20.’. They

were further informed that the council is considering strategies to raise registration

amongst students in university accommodation, where rates have been particularly

low. They were then told that the council decides to send a card to every unregistered

student living in university accommodation, and were presented with a picture of one

of three cards. These were replicas of the postcards sent out to students in the

Baseline, Monetary Loss and Monetary Gain 1 treatments (the only difference was

that the cards were cropped to cut off the OCC logo).

Subjects were then asked to evaluate ‘how socially appropriate most people would

think it would be for a student, having received this card, to register to vote or not to

register to vote.’. Earlier in the instructions, we had defined social appropriateness as

‘behaviour that you think most people would agree is the "correct" thing to do.

Another way to think about what we mean is that if someone were to behave in a

socially inappropriate way, then other people might be angry at them.’.70

We then asked subjects to evaluate the social appropriateness of each action (register

to vote, not register to vote) on a four-point scale, encompassing ‘very socially

appropriate’, ‘somewhat socially appropriate’, ‘somewhat socially inappropriate’, and

‘very socially inappropriate’. These evaluations were incentivised such that subjects

were encouraged to coordinate on the social norm: we told subjects we would

randomly select one of the two actions, and for this action, they would be eligible to

70 This follows the experimental instructions introduced by Krupka and Weber (2013). See Appendix D

for the experimental instructions and screenshots of the online survey.

149

receive a cash prize if their evaluation of its social appropriateness was the same as

that chosen by the most other subjects.71

4.2 Results

To analyse the data, we follow Krupka and Weber (2013) in transforming the

evaluations into numerical values. We assign evenly-spaced values of -1 for the rating

‘very socially inappropriate’, -0.33 for the rating ‘somewhat socially inappropriate’,

0.33 for the rating ‘somewhat socially appropriate’ and 1 for the rating ‘very socially

appropriate.’ We then calculate the mean ratings for each action by subjects exposed

to each treatment. The results are displayed in Figure 3.

We find that regardless of the treatment subjects are exposed to, registering to vote

tends to be seen as highly appropriate behaviour, while failing to register is generally

seen as inappropriate. However, there are also subtle but significant treatment

differences in peoples’ appropriateness judgments. In particular, subjects exposed to

the Monetary Gain treatment perceived registering to vote to be less appropriate than

did those exposed to the Baseline treatment (two tailed Fisher Randomisation Test, p

= 0.012).72 Moreover, failing to register to vote was perceived to be more

inappropriate by subjects exposed to the Monetary Loss treatment than it was by

those exposed to the Baseline treatment (p = 0.016). In contrast, we find no

significant differences in the perception of appropriateness of registering between

71 As the study was very short and conducted online, we paid only one out of every eight subjects,

determined retrospectively by a random lottery (subjects were informed about this at the

beginning of the experiment). Those chosen for payment received an automatic £10, plus a

further £30 if their evaluation matched that of the most other subjects in their treatment.

Although most subjects would not be paid, the study was still incentivised to a conventional level:

all subjects had a 1/8 chance of receiving between £10 and £40 for an approximately five-minute

task.

72 See Moir (1998) for a discussion of the randomisation test, and Kaiser and Lacy (2009) for

information on the Stata command used to apply it. In Study II, we correct our p-values for the fact

that we are testing multiple hypotheses relating to two interrelated dependent variables (the

appropriateness of registering to vote and not registering to vote). For each dependent variable,

we test Monetary Gain vs. Baseline and Monetary Loss vs. Baseline, a total of four tests. The

correction method we use is that of Benjamini and Hochberg (1995) and corrected p-values are

displayed in the text.

150

Monetary Loss and Baseline (p = 0.543), or the inappropriateness of non-registering

between Monetary Gain and Baseline (p = 0.718).

Figure 3: Social appropriateness of registration behaviour by treatment

Notes: Figure 3 shows the mean appropriateness ratings assigned to each

action (registering to vote, not registering to vote) by subjects exposed to the

Monetary Loss, Baseline and Monetary Gain 1 postcards. Mean ratings are

taken by assigning values of -1, -0.33, 0.33 and 1 for the ratings ‘very

inappropriate’, ‘somewhat inappropriate’, ‘somewhat appropriate’ and ‘very

appropriate’ respectively, and averaging the values for each action for all

participants exposed to a given treatment. Error bars indicate standard errors

of the mean.

Table 3 sheds light on how these treatment differences arise. It presents, for each

treatment, the distribution of subjects’ evaluations of the social appropriateness of

each possible action. It shows that the lower perceived social appropriateness of

registering to vote under Monetary Gain is driven by fewer subjects regarding

registering as ‘very socially appropriate’ relative to Baseline (50.8% versus 78.1%). It

can also be seen that the higher perceived social inappropriateness of failing to

register under the Monetary Loss treatment is driven by more subjects regarding non-

registering as ‘very socially inappropriate’ relative to Baseline (25.0% versus 10.9%),

and by fewer regarding it as ‘somewhat socially appropriate’ (13.3% versus 28.1%).

To summarise the results of Study II, we find that subjects exposed to the Monetary

Loss treatment perceived a relatively strong social norm against failing to register,

while subjects exposed to the Monetary Gain treatment perceived a relatively weak

-1

-.5

0

.5

1

Baseline MonetaryLoss

MonetaryGain

Baseline MonetaryLoss

MonetaryGain

Register to vote Not register to vote

So

cia

l a

pp

rop

ria

ten

ess (

± 1

SE

M)

151

social norm in favour of registering. This suggests that emphasising the fine for

failing to register strengthens the social norm against such behaviour, while offering

monetary incentives for successfully registering weakens the social norm demanding

such behaviour. Given the strong evidence from previous studies (see introduction)

that social norms influence economic behaviour, we propose that these normative

effects explain at least part of the success of the Monetary Loss treatment and

ineffectiveness of the Monetary Gain treatments.

Table 3: Distribution of social appropriateness evaluations

Appropriateness of registering to vote

Very socially

inappropriate

Somewhat

socially

inappropriate

Somewhat

socially

appropriate

Very socially

appropriate

Baseline 1.6 0 20.3 78.1

Monetary Loss 0 1.7 31.7 66.7

Monetary Gain 0 8.2 41.0 50.8

Appropriateness of not registering to vote

Very socially

inappropriate

Somewhat

socially

inappropriate

Somewhat

socially

appropriate

Very socially

appropriate

Baseline 10.9 54.7 28.1 6.3

Monetary Loss 25.0 58.3 13.3 3.3

Monetary Gain 9.8 60.7 23.0 6.6

Notes: Table 3 displays, by treatment, the percentage of subjects who evaluated registering to vote

(top) or not registering to vote (bottom) as very socially inappropriate, somewhat socially

inappropriate, somewhat socially appropriate, or very socially appropriate.

5. Conclusion

We investigated the effectiveness of different nudges aimed at raising voter

registration rates. A unique feature of our study is that it combines two types of

experiment: a natural field experiment to measure which nudge is most effective in

raising registrations, and an online experiment to investigate possible reasons why

different nudges may trigger different behavioural responses.

Our field experiment shows that highlighting to citizens the possibility of being fined

for failing to register is an effective strategy for public bodies to use. The effect we

identified by doing this was not only statistically significant, but also of a substantial

152

magnitude: having the fine emphasised made subjects around 1.5 times more likely to

register.

In contrast, we do not find evidence that offering financial inducements for

registration is an effective strategy, nor do we find an effect of non-monetary

interventions based on the foot-in-the-door technique (i.e., asking people to comply

with small requests in order to get them agree to a subsequent larger request). The

ineffectiveness of the latter can be explained by the fact that, of 3562 people who

were asked to agree with our small requests, only 13 did so. The effect had no chance

of taking hold, as we were unable to get our foot through the door in the first place.

The lack of success of our Monetary Gain treatments may represent another case of

economic incentives crowding out people’s intrinsic motivation to behave in a

socially constructive way, to add to those uncovered in previous research (e.g. Frey

and Oberholzer-Gee, 1997; Ariely et al., 2009; Gneezy et al., 2011; Bowles and

Polania-Reyes, 2012). We note that, in this respect, our study’s results differ from

those of John et al. (2015), who also offered entry into a cash lottery as a reward for

registering to vote in the UK. They found a small (approximately 4%) but significant

positive effect of monetary rewards on registration rates. We conjecture that a

plausible explanation for the contrast in results is that the maximum winnings offered

by John et al. (2015) were much larger than ours (between £1000 and £5000). Their

large material incentives may well have been enough to produce a positive effect,

even if they had to overcome a crowding out effect (Bowles and Polania-Reyes,

2012). A tentative conclusion could then be that, when offering cash for registration

or similar behaviours where there is danger of crowding out intrinsic motivations, one

must ‘pay enough or don’t pay at all’ (Gneezy and Rustichini, 2000). This would also

be consistent with Panagopoulos (2013), who found that financial inducements raised

voter turnout but only once they were sufficiently large. In our study registration rates

amongst those offered financial incentives were particularly low once the opportunity

for financial gain had passed; this may suggest– if our results generalise – that would-

be nudgers seeking to use monetary incentives to promote specific behaviours, in

environments where instrinsic motives can be crowded out, would be well warned

against subsequently turning off those financial incentives.

153

Finally, our online experiment sheds light on a possible explanation for the

contrasting effects that positive and negative monetary incentives have on voter

registration rates. We propose that a plausible explanation for these effects may be via

their influence on social norms. Our online experiment shows that emphasising the

fine strengthens the perception that failing to register is socially inappropriate, while

offering money for registering weakens the perception that registering is socially

appropriate. We interpret this as evidence that social norms are a significant factor

determining voter registration, a finding which is consistent with other recent

experimental literature pointing to the importance of social norms as drivers of a wide

range of behaviours (e.g. Burks and Krupka, 2012; Gachter et al., 2013; Krupka and

Weber, 2013; Banerjee, 2016; Barr et al., 2016; Kimbrough and Vostroknutov, 2016;

Krupka et al., 2016). A key novel contribution of our study in relation to this

literature is in identifying the potentially important role of norms in determining the

effectiveness of different types of nudge intervention.

154

Acknowledgements

This research was funded by the Economic and Social Research Council via the

Network for Integrated Behavioural Sciences (Award No. ES/K002201/1), and by the

Centre for Decision Research and Experimental Economics within the University of

Nottingham’s School of Economics. The research was done in collaboration with

Oxford City Council’s Electoral Services team, in particular Suzette Starmer and

Martin John; and we received important assistance in Nottingham from Suzanne

Robey. We received helpful input during the course of the project, and after

presentations at Nottingham, from, amongst others, Abigail Barr, Robin Cubitt,

Matthias Dahm, Gianni De Fraja, Markus Eberhardt and Konstantinos Tatsiramos.

155

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Online Appendices

Appendix A: Postcard Intervention in Study I

Baseline Treatment

Monetary Loss treatment

160

Monetary Gain Treatment 1

Monetary Gain Treatment 2

161

Non-monetary Treatment 1

Non-monetary Treatment 2

162

Appendix B: Details on assignment to treatment

Table B1 presents a breakdown, by university and place of residence, of the subjects

assigned to each treatment. As stated in Section 2.3, we randomised assignment to

treatment at the building level. For the University of Oxford, all students living in a

single college were assigned to the same treatment. Two university-owned buildings

(140 Walton St. and Castle Mill) which house students from various colleges were

treated as if they were colleges, with common treatment assignment within each

building. Two colleges, St. Cross and Brasenose, share a residence building (the St.

Cross/Brasenose Annex). St. Cross and Brasenose were assigned to the same

treatment. For the purposes of clustering in our regression analysis, 140 Walton St.,

Castle Mill and the St. Cross/Brasenose Annex are all treated as independent units of

residence.

For Oxford Brookes University, all students living in a single hall of residence were

assigned to the same treatment, with the exception that two very large halls, Cheney

and Clive Booth, which were split into several units of assignment. Cheney and Clive

Booth are naturally split into discrete residence blocks, so we subdivided them on this

basis, ensuring maximum geographical distance between the subjects in these halls

assigned to different treatments. For the purposes of clustering in our regression

analysis, each subdivision that we split Cheney and Clive Booth into is treated as one

unit of residence.

Beyond balancing assignment at the university level, the randomisation was also

subject to the following constraints. Each treatment had to feature a mixture of large

and small residence units; we ensured this by splitting the residence units into pools

based on size, and assigned one unit from each pool to each treatment. Each treatment

also had to feature a mixture of ancient and modern University of Oxford colleges, to

the extent that the average college age in all treatments had to be within 200 years.

Finally, the total number of subjects assigned to the largest treatment had to be no

more than 15% greater than the number assigned to the smallest. We repeated the

randomisation until it produced an assignment which met all the above criteria.

Our randomisation strategy was imperfectly implemented. Mailing errors resulted in

some subjects being assigned to treatments we did not intend them to be (in italics in

163

Table B1). This explains why 16 students in Lincoln College were assigned to the

Monetary Loss treatment, while the other 132 were assigned to the Baseline

treatment; and why 6 Kellogg College students were assigned to Non-Monetary

Treatment 2, with the other 11 were assigned to the Monetary Loss Treatment. As a

robustness check, we re-ran our analysis excluding Lincoln and Kellogg from our

dataset. All our results are robust and change only marginally.

164

Table B1: Breakdown of treatment assignment by university and college/hall

Treatment College/hall Number

assigned

Percentage of total

assigned to treatment

Baseline University of Oxford

Keble

Magdalen

St Hugh’s

Lincoln

Corpus Christi

Harris Manchester

All Souls

Oxford Brookes

Clive Booth

Paul Kent

Total

889

206

201

200

132

120

26

4

304

153

151

1193

74.52

17.27

16.85

16.76

11.06

10.06

2.18

0.34

25.48

12.82

12.66

100.00

Monetary Loss University of Oxford

St. Catherine’s

Jesus

Pembroke

University College

St. Peter’s

Green Templeton

Lincoln

Kellogg

140 Walton Street

Oxford Brookes

Clive Booth

Warneford

Total

1026

254

188

188

147

146

71

16

11

5

331

187

144

1357

75.61

18.72

13.85

13.85

10.83

10.76

5.23

1.18

0.81

0.37

24.39

13.78

10.61

100.00

Monetary Gain 1 University of Oxford

Worcester

Hertford

Trinity

Oriel

Mansfield

Linacre

Oxford Brookes

Clive Booth

Cheney

940

311

236

154

140

74

25

310

162

128

75.20

24.88

18.88

12.32

11.20

5.92

2.00

24.80

14.56

10.24

165

Total 1250 100.00

Monetary Gain 2 University of Oxford

St. Edmund

Merton

The Queen’s

St. Hilda’s

Nuffield

Wycliffe

Oxford Brookes

Clive Booth

Cheney

Total

1044

398

253

209

156

14

14

273

168

105

1317

79.27

30.22

19.21

15.87

11.85

1.06

1.06

20.73

12.76

7.97

100.00

Non-monetary 1 University of Oxford

Christ Church

New College

Wadham

Castle Mill

Exeter

Brasenose

St. Cross/Brasenose

St. Cross

Oxford Brookes

Crescent

Cheney

Total

947

199

195

182

160

80

74

29

28

315

212

103

1262

75.04

15.77

15.45

14.42

12.68

6.34

5.86

2.30

2.22

24.96

16.80

8.16

100.00

Non-monetary 2 University of Oxford

St. Anne’s

Balliol

St. John’s

Somerville

Lady Margaret Hall

Wolfson

Kellogg

Oxford Brookes

Clive Booth

Cheney

Total

979

216

192

167

164

162

72

6

321

182

139

1300

75.31

16.62

14.77

12.85

12.62

12.46

5.54

0.46

24.69

14.00

10.69

100.00

166

Appendix C: Additional Analyses

Figure C1: Cumulative registration rates by treatment (uncombined)

Notes: Figure C1 shows, on a daily basis between the start of the intervention

on March 9 and the registration deadline on April 20, the amount of registered

students in the treated buildings, as a fraction of all students in these buildings

who had been unregistered on January 2.

Treatmentintervention

Lotterydeadline

0

.05

.1

.15

.2

.25

.3

.35

Reg

istr

ation

ra

te

-1 1 5 9 13 17 21 25 29 33 37 41

Days since intervention

Baseline Monetary Loss

Monetary Gain 1 Monetary Gain 2

Non-Monetary 1 Non-Monetary 2

167

Table C1: The effects of treatments on registration rates (uncombined)

Dependent variable = 1 if registered,

0 if not

Logistic Regression

Before

Intervention

(Jan 8 – March 8)

After

Intervention

(March 9 – April 20)

Monetary Loss 0.901 1.565**

(0.223) (0.286)

Monetary Gain 1 1.037 0.707

Monetary Gain 2

(0.246)

0.935

(0.251)

(0.233)

0.706

(0.216)

Non-Monetary 1 0.869 0.943

(0.298) (0.168)

Non-Monetary 2 1.068 1.136

(0.228) (0.243)

Brookes Student 0.394*** 0.671***

(0.064) (0.084)

Constant 0.113*** 0.238***

(0.020) (0.039)

Wald-tests (p-values):

Monetary Gain 1 = Monetary Gain 2

0.682 0.996

Non-Monetary 1 = Non-Monetary 2 0.514 0.226

N 8397 7679

Notes: Reported are odds ratios. Robust standard errors clustered at the

residence unit are in parentheses. *** p<0.01, ** p<0.05, * p<0.1. The table

further includes the p-values from Wald tests of the hypothesis that the

coefficients differ between the two types of Monetary Gain treatments and the

two types of the Non-Monetary treatments.

Duration analysis

To test the robustness of the results in Table 1, for the post-intervention period we

apply duration analysis to examine the data underlying Figure 2 by taking into

account the time it takes an individual to register after having received our postcards.

Specifically, we use a Cox proportional hazard approach to model the duration until

an individual registers. Estimated hazard ratios are reported in model (1) in Table C2.

In line with the results from the logistic regression, we find a positive and significant

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effect of the Monetary Loss dummy. The hazard ratio of 1.656 indicates that - for

those in the Monetary Loss treatment - the probability of registering on a certain date

(conditional on not having been registered before) is 65.6% larger than in Baseline.

The corresponding hazard ratios for the Monetary Gain and Non-Monetary dummies,

in contrast, are not significantly different from 1, indicating no difference in the

conditional probability of registering relative to Baseline for these two treatments.

The robustness of the result in Table 2 is also tested using a Cox proportional hazard

approach (model (2) in Table C2), which models the duration until an individual

registers within the two post-intervention time periods, before and after the lottery

deadline has passed. In line with the result from model (1) in Table 2, we find that the

Monetary Gain dummy is insignificant (with a hazard ratio of 1.264), indicating that

there are no pronounced differences in the conditional probability of registering

between Baseline and Monetary Gain in the period where monetary incentives for

registering are still in place. Furthermore, in line with the results from model (2) in

Table 2 we find a significant interaction effect between the Monetary Gain dummy

and a dummy for the post lottery deadline period. This indicates that the probability

of registering (conditional on not having been registered before) in Monetary Gain

relative to Baseline reduces once the deadline for entry into the lottery has passed.

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Table C2: Duration analysis

Dependent variable Duration to registration

(1) (2)

After Intervention

(Mar 9 – Apr 20)

Monetary Loss 1.656**

(0.302)

Monetary Gain 0.782 1.264

(0.167) (0.425)

Non-Monetary 1.019

Monetary Gain x Post deadline

(0.165)

0.549**

(0.147)

Controls Yes Yes

N 7679 3760

Notes: The table reports hazard ratios from estimations based on Cox proportional hazard models.

Note that a ratio greater than 1 implies a positive effect, whereas a ratio smaller than 1 implies a

negative effect. The dependent variable is the duration until an individual registers (i.e. the time

between our treatment intervention and the date at which an individual registers). In model (2) only

data from Monetary Gain and Baseline are included. Robust standard errors clustered at the residence

unit are reported in parentheses. Significance levels: *** p<0.01, ** p<0.05, * p<0.1

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Appendix D: Screenshots of Study II

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Chapter Five: Conclusion The first two substantive chapters of this dissertation (Chapters 2 and 3) are primarily

focused on how and why the strength of discrimination varies across contexts. The

most important results of Chapter 2 were: that lab experiments have found stronger

discrimination between some types of identity groups than others; and that, in

particular, minimal group experiments find stronger discrimination than one might

expect. This finding was the central focus of investigation in Chapter 3. Here, we

proposed and found support for one possible explanation for the result: that

discrimination is perceived to be less socially inappropriate in some circumstances

than in others, and that in those circumstances where it is less socially inappropriate

people are more willing to engage in discrimination.

There is certainly scope for more future research on the relationship between

discrimination and social norms. Field experiments could, for instance, investigate the

effects on discrimination of nudges designed to reduce the social appropriateness of

discriminating. There is also scope for more research investigating other possible

reasons for contextual differences in levels of discrimination – in particular, why lab

experiments yield relatively high levels of discrimination across minimal groups but

relatively low levels across ethnic, national or religious groups. As I discuss in the

first and second chapters, these phenomena may suggest lab experiments face

difficulties in estimating levels of discrimination that are generalizable to the outside

world. The external generalizability of lab estimates of discrimination could be

studied by designing experiments to measure discrimination in both lab and field

contexts while carefully holding other features of the decision-making context

constant (see Stoop et al, 2012, and Stoop, 2014, for experiments following this

approach in other research areas).

Chapter 4 of the dissertation departs from the topic of discrimination: the main focus

here is on nudging in public policy. However, it also maintains an emphasis on social

norms. Both Chapters 2 and 3 provide evidence to support the notion that social

norms play a role in determining behavioural regularities. The norm-elicitation

method we use in both cases – that of Krupka and Weber (2013) – is being widely

adopted by experimental economists and there is, no doubt, scope for future research

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into the reliability of the method itself, as well as into other methods of measuring

social norms. In particular, the Krupka-Weber method’s use of monetary incentives to

encourage coordination on the social norm has received some attention (e.g. Vesely,

2015) but further research could provide greater clarity on the effect of this design

feature.

Chapter 4 provides a case where the context dependence of social norms can be

exploited to achieve a policy goal. With current interest in social norms high,

policymakers are increasingly aware of the possibilities offered by nudges harnessing

the effects of social norms (e.g. Ayres et al, 2012; Behavioural Insights Team, 2011).

Such social nudging could be implemented across a very wide range of policy

domains. For instance, governments interested in reducing discrimination may find

campaigns aimed at strengthening the taboo nature of such behaviour to be effective

tools. Of course, we should have no presumptions about the preferences of

policymakers. Indeed, those who wish to see discrimination eliminated may have as

much reason to fear the potential for policymakers to influence social norms as to be

thankful for it; it is, for instance, quite plausible that the apparent efforts of current

prominent politicians around the world to normalise certain forms of discrimination

could lead to an upsurge in their prevalence.

References

Ayres, I., Raseman, S., & Shih, A. (2012). Evidence from two large field experiments

that peer comparison feedback can reduce residential energy usage. Journal of Law,

Economics, and Organization, ews020.

Behavioural Insights Team (2011). Behaviour change and energy use. London:

Cabinet Office.

Krupka, E. L., & Weber, R. A. (2013). Identifying social norms using coordination

games: Why does dictator game sharing vary?. Journal of the European Economic

Association, 11(3), 495-524.

Stoop, J. (2014). From the lab to the field: envelopes, dictators and

manners. Experimental Economics, 17(2), 304-313.

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Stoop, J., Noussair, C. N., & Van Soest, D. (2012). From the lab to the field:

Cooperation among fishermen. Journal of Political Economy, 120(6), 1027-1056.

Veselý, S. (2015). Elicitation of normative and fairness judgments: Do incentives

matter?. Judgment and Decision Making, 10(2), 191.

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Acknowledgements

I would like to finally conclude this dissertation by thanking my PhD supervisors,

Abigail Barr and Daniele Nosenzo. I am incredibly grateful for all your tireless work

in supporting me throughout the course of my studies in Nottingham. I could not have

asked for more wonderful supervisors. I am also very grateful to Felix Kölle and

Chris Starmer, who co-authored the third chapter. My PhD was funded by the

Network for Integrated Behavioural Science. I am particularly grateful to Robin

Cubitt, who assisted me in my application for this grant. Finally, I am indebted to all

staff and fellow students in the School of Economics, every one of whom has

contributed to my learning here.